In March of 2022, Mike Pratt officially stepped down as Associate Editor, a position he has held at ASQ for over twelve years. In this time, he has managed the review process for hundreds of papers. On this occasion, Mike responded to the Blog Board’s questions about what he has learned about the role of reviewing in advancing the field, common challenges faced by qualitative papers, and the range of paths to a scholarly contribution.
1. Many papers published in ASQ thank the associate editor and anonymous reviewers for their role in the review process. What does an associate editor do? Are there any ways that you view the role differently now than when you began as associate editor at ASQ?
Mike: An associate editor at ASQ is responsible for reading manuscripts, finding appropriate reviewers for it, and when the reviews are done, making an editorial decision: reject, revise, provisionally accept or accept. There are also times when I answer questions from the authors after a decision has been made. In those interactions, I can clarify what I meant in a decision letter. I have also been asked what a specific reviewer meant in a comment. Unfortunately, I most often don’t know what the reviewer meant either. Unless the reviewer used the “comments to the editor” box and clarified a given comment, I only have the information that the authors have.
If authors reach out to me, they may also ask if a specific direction they want to take is consistent with my editorial letter and with what the reviews have suggested. I can often give some high-level advice, but I always tell authors that I cannot guarantee that any given approach they take will be well-received by the reviewers or result in a favorable decision.
Sometimes people ask if associate editors have to have the head editor’s (which we just call the editor) approval on a manuscript decision. Unlike some other journals, the editor does not intervene or have to “sign off” on a decision letter. So, AEs serve as the author’s editor (or “handling editor”) for a manuscript. [In case you are curious, the editor does all that an AE does and more, such as thinking about the strategic direction of the journal.]
In the over twelve years I have been an AE at ASQ, the role itself has been very consistent. I worked under three different editors, all of whom had a very similar way of viewing the AE role. However, how I perceive the role has changed over time. ASQ is a very selective journal, and it is difficult to have to reject a lot of papers. After a particularly taxing stretch of writing rejection letters, I began to rethink my role. In addition to getting papers published in ASQ, I thought about being an AE more broadly: to help make every paper that undergoes the review process better than if it had not undergone the review process at all. Unfortunately, not everyone who has undergone a review process feels that the paper is better off for it (and I have had experiences like that myself as an author submitting to other journals). This sentiment is especially true if the paper is rejected. Thus, I tried (and I am sure I failed at times) to make sure that whatever my editorial decision was, that the authors benefited in some way from submitting their paper to ASQ.
As an important aside, a rejection does not mean that the paper is ultimately a failure. Sometimes authors just submit papers too soon (i.e., they are too underdeveloped). Thus, my goal is to facilitate the progress of a paper in the field— not just at ASQ.
2. What has been your favorite part of working as an associate editor at ASQ?
I absolutely love to see a paper develop through the review process. To see authors take some good, but perhaps not well-executed, ideas in round one and develop them into a field-changing paper is quite honestly an amazing experience. In that role, I like the image of a midwife. To paraphrase John Heider in his book The Tao of Leadership, my job is to assist the author in the “birth” of their paper; and like a midwife, my job is to be supportive, knowing that it is “their baby” and the authors are doing the tough work in the creation process. Just being part of this process is absolutely incredible.
As noted in the previous answer, my hope is to make papers better through the review process, no matter what the outcome. I have been amazed at the number of kind, thoughtful and appreciative emails I have received from authors whose papers were rejected. I have learned a lot from these authors, and now when I am an author, I try to follow their example. Some authors have even traced their process at ASQ to facilitating their paper’s acceptance at another journal. That is also deeply gratifying, for our ultimate responsibility is to the field.
3. In your opinion, how does reviewing and serving on editorial boards fit into a scholarly career?
Reviewing is the lifeblood of our profession. We simply cannot function without reviewers. For many scholars in the field, what we publish is key to how we are evaluated annually, whether or not we are promoted, and is the basis of our reputation. And we cannot publish if there are no reviewers. Therefore, I see reviewing as the obligation of anyone who has ever submitted a manuscript to a journal. It is our way of paying back and keeping the profession going. I realize that there are many ways to serve the field, and some may not wish to join editorial boards or become AEs or editors. However, my personal belief is that everyone should review during their careers.
However, reviewing is not just an obligation. It also has benefits for the reviewer. To begin, I have found that reviewing (and editing) has also made me a much better scholar and writer. Participating in the review process by doing reviews— and by reading the reviews of others as well as the editor’s letter— is very helpful for understanding how to put a paper together, including what pitfalls to avoid. In addition, being on editorial boards is a great way to network, and looks great when one is coming up for promotion and tenure.
For those who do not know how to get on an editorial board, you are often invited when you review several manuscripts in a year (e.g., six or more— though there is no magic number) for a specific journal, and do “high quality” reviews. Every time you do a review for ASQ (as well as many other journals), your review is ranked in terms of its quality. You can often tell if your review is of high quality if the editor refers to it in their letter.
In sum, being a reviewer is an important obligation to fulfill on behalf of the field. In addition, it can benefit the reviewer as well by improving skills, creating networks, and signaling professional visibility that can facilitate one’s advancement.
4. Having served as the handling editor for numerous qualitative papers, what do you see consistently as challenges in qualitative submissions, and what advice would you offer to qualitative researchers about writing up their work?
The challenges that qualitative papers face can be categorized in terms of framing, methods, findings and contributions. There are a lot of them so I will try to stick with the biggest ones in each category.
Framing. By far the biggest issue with framing is inadequately motivating one’s paper. Probably the most common and least effective way to frame an inductive study is by saying that no (meaningful) literature exists in your area of study. “No one else has done this but I will!” Unfortunately, this says nothing about why a study should be pursued. We know little about a leader’s sock preferences, but who cares if we know more (and this is from someone whose first paper was on organizational dress!)? A similar and equally inadequate motivation is that existing theory is not “nuanced” or complex enough. If I had the power to expunge one word from academic language, it might just be “nuance.” All theory, by its nature, is abstract and thus can be made more complex. You must, therefore, be able to argue why it is theoretically important to make an existing theory more complex. Ideally, authors should be able to argue that extant literature is not only incomplete, but that our current understanding is likely flawed.
More generally, I recommend that authors be cognizant of what is figure and what is ground in their framing. To illustrate, perhaps you found that individuals who work in geographically distributed online teams have an ambivalent relationship with their employing organization. Do you frame your paper in terms of ambivalence, identification, commitment, person-organization fit, or something else? Moreover, within extant theory, which is the most important? Stringing together a list of theories is often confusing. One way to avoid this issue is to answer the question, “who do you see as your primary audience?” Using the example above, should I frame the manuscript as an ambivalence paper that discusses the role of attachment? Alternatively, is this primarily a paper about how individuals attach to their organizations and the role ambivalence might play in it? Although both may contain similar theories, one is a paper about ambivalence and the other is about attachment.
Methods. I think the biggest issue with methods is that too many people say “what they did” without sufficiently stating “why they did it this way.” Making matters worse, even their description of “what they did” tends to be quite generic (e.g., I used a grounded theory approach to analyzing my data using open, axial, and selective coding). I would suggest that authors do more to discuss why they did what they did in light of their research question. For example, if you are asking a process-related question, how did you get a process in your analysis? Although you should not take the reader on a blow-by-blow rendition of everything you did (including those blind alleys that did not work out), it is important to give the reader a general sense of what your logic was for choosing particular analytic moves (e.g., using axial versus focused coding in grounded theory), and how you enacted these choices.
Findings. Regarding findings, the challenge here is to have a clear storyline. Oftentimes the “connective tissue” linking the various parts of one’s findings is missing. The author knows how it all goes together because they have lived with the data for a long time. But for those who are newer to the paper, the organizational logic is not clear.
Critical to having a clear storyline is knowing what the author thinks is the most important set of findings. There are times when authors are not sure, so they throw a bunch of findings at the reviewer/reader— kind of like throwing spaghetti against the wall and seeing what sticks. The issue here is that reviewers won’t know what to hold onto (similar to the figure/ground issue in framing). What often happens then is that reviewers will tend to gravitate towards different findings— often related to what their areas of expertise are. The end result is that the author receives very conflicting advice for how to move the paper forward.
Having a clear storyline also means that your data fit with your arguments and that you are neither simply telling the reviewers what you found (without providing ample evidence) or hoping that the data will speak for themselves (they do not).
Contribution. Finally, when laying out the contribution in a discussion section, one of the biggest issues I see is authors simply restating what they found. This is especially problematic for papers where the authors have framed the paper as “no one else has done this.” If you do this, one might be tempted to say in your contributions, “no one else has done this but I have!” This statement is typically followed by a repetition of findings. I am not saying that summarizing findings is necessarily bad— just that the summary cannot be your main contribution. Another common mistake is arguing for making a lot of small (incremental) contributions, often across a variety of literatures, rather than arguing for a “big” contribution. Unfortunately, a lot of small contributions do not add up to a big one. I’ll return to contributions in the next answer.
Before I move on, however, it is important to note the challenges often depend on where you are in the review process. If you get a first-round revision, I often tell authors that your challenge is to “tear down your house and rebuild” your paper. This means that the author has a strong foundation (often good data) but there are framing and methodological issues and, by consequence, issues with contribution. What many authors do is to try to incorporate all of the feedback from the reviewers in a very piecemeal fashion. For example, if Reviewer #1 wants you to add something on goal-setting theory, Reviewer #2 on trust, and Reviewer #3 on conflict, simply adding these theories in is likely to muddle your storyline and confuse your figure/ground dynamics. Continuing the metaphor, it’s like a house that has been renovated by adding on rooms but it is not clear why there are so many rooms or how they are connected. Better to rebuild the paper from whatever your foundation is.
It may also help authors when reading a review to separate out issues from suggestions. An issue with your paper may be theory-data alignment. A suggestion for fixing that misalignment might be utilizing a particular theory. The author’s job is to address the issues raised, not to incorporate each and every reviewer suggestion. What authors will often find is that the issues raised are often pretty consistent across reviewers— even if how to fix them is not (i.e., the suggestions). When rebuilding, doing it with an eye towards addressing issues and not suggestions will help you avoid the “too many rooms” problem.
If you continue in the review process, I often change my metaphor to “smelting ore.” Smelting involves removing impurities from an ore to get at the metal. Ideally, by the second round of the review process, you know what is important (and the reviewers agree) and the issue is filtering out extraneous materials to make the core arguments shine. Failure can occur here when authors cannot let go of extraneous material (it is harder than you think to let go of cherished arguments), and when ultimately there is not enough “metal” (e.g., there is not enough data to support the claims that were deemed most important).
5. In doing this work, has your perspective grown or changed on what represents a contribution to a field of organizational inquiry?
Yes, I think my perspective on what a contribution is has grown. As noted earlier, part of this learning is better recognizing what a significant contribution is not (e.g., not a summary or a string of small contributions). Part of my learning has also come from being at ASQ where a significant contribution is often referred to as “changing the nature of the conversation” of whatever topic your study is about. I admit I have wrestled a lot with what “changing the nature of the conversation” means. It is not only opaque but, as one reviewer put it, it can sound pretty arrogant. So I’ll say what it means for me— knowing that others are welcome to disagree and with the standard disclaimer that I am not speaking on behalf of the journal.
I think there are a few ways to make a contribution. The one I think most people think of is to write something that causes readers to see a field in a new way. Some can incite something akin to a Copernican shift (the earth revolves around the sun, not the other way around). Such truly revolutionary papers are exceedingly rare. Fortunately, it’s not the only way to make a contribution. Sometimes it is showing that something we didn’t recognize really matters. It is hard to imagine understanding group behavior before knowing about emotional contagion (Sigal Barsade) or psychological safety (Amy Edmondson). At other times, it is challenging what we think we know— such as an assumption that organizations are largely tightly coupled (Karl Weick). We can change the nature of the conversation in a more synthetic way as well: bridging areas of knowledge that were previously separate (such as Herminia Ibarra’s work connecting identity and socialization via provisional selves). Personally, I think the great articles are the ones that stick with me. These articles create new connections among ideas in my head, make me excited to think about an area I was not excited about before, or cause me to think about my own research in a new way. I am sure there are others.
Although I have learned more about paths to a contribution, ascertaining whether a particular paper has made enough of a contribution (i.e., has gone far enough down a particular path) remains challenging. There are many things to consider. To illustrate, sometimes simply moving the needle on a well-established field may be as significant as a paper that upends an emerging field. Over time, I have learned to trust the wisdom of reviewers who are experts in the field, as well as my own judgements having edited hundreds of articles.
I also realize that as a human being, I may not always get it right. On that, I take some comfort in knowing that the field itself will ultimately judge which papers are truly transformative.