Description
Summarize and Reaction the readings (1,2,3,4,5)
Summarize the readings (Research Design and Discussion):
1. The foundations of research: chapter 7 (Pages 157 – 189)
2. Your research project: chapter 7 (pages 305 – 408)
3. Bono, J. E., & McNamara, G. (2011). From the Editors_Publishing in AMJ-Part 2: Research Design. Academy of Management Journal, 54(4), 657-660.
4. Zhang, Y., & Shaw, J. D. (2012). Publishing in AMJ—Part 5: Crafting the methods and results. Academy of Management Journal. 8-12.
5. Geletkanycz, M., & Tepper, B. J. (2012). Publishing in AMJ–part 6: Discussing the implications.
***There are two main parts to the summary: ***
1. Summary of each chapter/article: Includes Title of Article, Author(s), Source, and Date of Article using APA style. In your OWN WORDS describe what the article is about, with major details or points, and should be easy to read (i.e. interesting and flow well!) (shows strong evidence of knowledge and understanding of the readings)
2. Reaction: Briefly describe the implications to scholars in academia (so what? in what ways you can utilize the ideas in the readings in your professional development as a scholar).
***Use easy words and easy Sentence***
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娀 Academy of Management Journal
2011, Vol. 54, No. 4, 657–660.
FROM THE EDITORS
PUBLISHING IN AMJ—PART 2: RESEARCH DESIGN
Editor’s Note:
This editorial continues a seven-part series, “Publishing in AMJ,” in which the editors give suggestions and advice for
improving the quality of submissions to the Journal. The series offers “bumper to bumper” coverage, with installments
ranging from topic choice to crafting a Discussion section. The series will continue in October with “Part 3: Setting the
Hook.”- J.A.C.
Most scholars, as part of their doctoral education,
take a research methodology course in which they
learn the basics of good research design, including
that design should be driven by the questions being
asked and that threats to validity should be avoided.
For this reason, there is little novelty in our discussion of research design. Rather, we focus on common
design issues that lead to rejected manuscripts at
AMJ. The practical problem confronting researchers
as they design studies is that (a) there are no hard and
fast rules to apply; matching research design to research questions is as much art as science; and (b)
external factors sometimes constrain researchers’
ability to carry out optimal designs (McGrath, 1981).
Access to organizations, the people in them, and
rich data about them present a significant challenge
for management scholars, but if such constraints
become the central driver of design decisions, the
outcome is a manuscript with many plausible alternative explanations for the results, which leads
ultimately to rejection and the waste of considerable time, effort, and money. Choosing the appropriate design is critical to the success of a manuscript at AMJ, in part because the fundamental
design of a study cannot be altered during the revision process. Decisions made during the research
design process ultimately impact the degree of confidence readers can place in the conclusions drawn
from a study, the degree to which the results provide a strong test of the researcher’s arguments, and
the degree to which alternative explanations can be
discounted. In reviewing articles that have been
rejected by AMJ during the past year, we identified
three broad design problems that were common
sources of rejection: (a) mismatch between research
question and design, (b) measurement and operational issues (i.e., construct validity), and (c) inappropriate or incomplete model specification.
and macro research. Rejection does not happen because such data are inherently flawed or because
reviewers or editors are biased against such data. It
happens because many (perhaps most) research questions in management implicitly— even if not framed
as such—address issues of change. The problem with
cross-sectional data is that they are mismatched with
research questions that implicitly or explicitly deal
with causality or change, strong tests of which require
either measurement of some variable more than once,
or manipulation of one variable that is subsequently
linked to another. For example, research addressing
such topics as the effects of changes in organizational
leadership on a firm’s investment patterns, the effects
of CEO or TMT stock options on a firm’s actions, or
the effects of changes in industry structure on behavior implicitly addresses causality and change. Similarly, when researchers posit that managerial behavior affects employee motivation, that HR practices
reduce turnover, or that gender stereotypes constrain
the advancement of women managers, they are also
implicitly testing change and thus cannot conduct
adequate tests with cross-sectional data, regardless of
whether that data was drawn from a pre-existing data
base or collected via an employee survey. Researchers
simply cannot develop strong causal attributions
with cross-sectional data, nor can they establish
change, regardless of which analytical tools they use.
Instead, longitudinal, panel, or experimental data are
needed to make inferences about change or to establish strong causal inferences. For example, Nyberg,
Fulmer, Gerhart, and Carpenter (2010) created a panel
set of data and used fixed-effects regression to model
the degree to which CEO-shareholder financial alignment influences future shareholder returns. This data
structure allowed the researchers to control for crossfirm heterogeneity and appropriately model how
changes in alignment within firms influenced shareholder returns.
Our point is not to denigrate the potential usefulness of cross-sectional data. Rather, we point out
the importance of carefully matching research design
to research question, so that a study or set of studies
Matching Research Question and Design
Cross-sectional data. Use of cross-sectional data
is a common cause of rejection at AMJ, of both micro
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is capable of testing the question of interest. Researchers should ask themselves during the design stage
whether their underlying question can actually be
answered with their chosen design. If the question
involves change or causal associations between variables (any mediation study implies causal associations), cross-sectional data are a poor choice.
Inappropriate samples and procedures. Much organizational research, including that published in
AMJ, uses convenience samples, simulated business
situations, or artificial tasks. From a design standpoint, the issue is whether the sample and procedures
are appropriate for the research question. Asking students with limited work experience to participate in
experimental research in which they make executive
selection decisions may not be an appropriate way to
test the effects of gender stereotypes on reactions
to male and female managers. But asking these same
students to participate in a scenario-based experiment in which they select the manager they would
prefer to work for may present a good fit between
sample and research question. Illustrating this notion
of matching research question with sample is a study
on the valuation of equity-based pay in which Devers,
Wiseman, and Holmes (2007) used a sample of executive MBA students, nearly all of whom had experience with contingent pay. The same care used in
choosing a sample needs to be taken in matching
procedures to research question. If a study involves
an unfolding scenario wherein a subject makes a series of decisions over time, responding to feedback
about these decisions, researchers will be well served
by collecting data over time, rather than having a
series of decision and feedback points contained in a
single 45 minute laboratory session.
Our point is not to suggest that certain samples
(e.g., executives or students) or procedures are inherently better than others. Indeed, at AMJ we explicitly
encourage experimental research because it is an excellent way to address questions of causality, and we
recognize that important questions— especially those
that deal with psychological process— can often be
answered equally well with university students or
organizational employees (see AMJ’s August 2008
From the Editors [vol. 51: 616 – 620]). What we ask of
authors—whether their research occurs in the lab or
the field—is that they match their sample and procedures to their research question and clearly make the
case in their manuscript for why these sample or
procedures are appropriate.
Measurement and Operationalization
Researchers often think of validity once they begin operationalizing constructs, but this may be too
late. Prior to making operational decisions, an au-
August
thor developing a new construct must clearly articulate the definition and boundaries of the new construct, map its association with existing constructs,
and avoid assumptions that scales with the same
name reflect the same construct and that scales with
different names reflect different constructs (i.e., jingle
jangle fallacies [Block, 1995]). Failure to define the
core construct often leads to inconsistency in a manuscript. For example, in writing a paper, authors may
initially focus on one construct, such as organizational legitimacy, but later couch the discussion in terms
of a different but related construct, such as reputation
or status. In such cases, reviewers are left without a
clear understanding of the intended construct or its
theoretical meaning. Although developing theory is
not a specific component of research design, readers
and reviewers of a manuscript should be able to
clearly understand the conceptual meaning of a construct and see evidence that it has been appropriately
measured.
Inappropriate adaptation of existing measures.
A key challenge for researchers who collect field
data is getting organizations and managers to comply, and survey length is frequently a point of concern. An easy way to reduce survey length is to
eliminate items. Problems arise, however, when
researchers pick and choose items from existing
scales (or rewrite them to better reflect their unique
context) without providing supporting validity evidence. There are several ways to address this problem. First, if a manuscript includes new (or substantially altered measures), all the items should be
included in the manuscript, typically in an appendix. This allows reviewers to examine the face validity of the new measures. Second, authors might
include both measures (the original and the shortened versions) in a subsample or in an entirely
different sample as a way of demonstrating high
convergent validity between them. Even better
would be including several other key variables in
the nomological network, to demonstrate that the
new or altered measure is related to other similar
and dissimilar constructs.
Inappropriate application of existing measures. Another way to raise red flags with reviewers is to use existing measures to assess completely
different constructs. We see this problem occurring
particularly among users of large databases. For
example, if prior studies have used an action such
as change in format (e.g., by a restaurant) as a measure of strategic change, and a submitted paper uses
this same action (change in format) as a measure of
organizational search, we are left with little confidence that the authors have measured their intended construct. Given the cumulative and incremental nature of the research process, it is critical
2011
Bono and McNamara
that authors establish both the uniqueness of their
new construct, how it relates to existing constructs,
and the validity of their operationalization.
Common method variance. We see many rejected
AMJ manuscripts in which data are not only crosssectional, but are also assessed via a common method
(e.g., a survey will have multiple predictor and criterion variables completed by a single individual).
Common method variance presents a serious threat to
interpretation of observed correlations, because such
correlations may be the result of systematic error
variance due to measurement methods, including
rater effects, item effects, or context effects. Podsakoff, MacKenzie, Lee, and Podsakoff (2003) discussed common method variance in detail and also
suggested ways to reduce its biasing effects (see
also Conway & Lance, 2010).
Problems of measurement and operationalization
of key variables in AMJ manuscripts have implications well beyond psychometrics. At a conceptual
level, sloppy and imprecise definition and operationalization of key variables threaten the inferences that can be drawn from the research. If the
nature and measurement of underlying constructs
are not well established, a reader is left with little
confidence that the authors have actually tested the
model they propose, and reasonable reviewers can
find multiple plausible interpretations for the results. As a practical matter, imprecise operational
and conceptual definitions also make it difficult to
quantitatively aggregate research findings across
studies (i.e., to do meta-analysis).
Model Specification
One of the challenges of specifying a theoretical
model is that it is practically not feasible to include
every possible control variable and mediating process, because the relevant variables may not exist in
the database being used, or because organizations
constrain the length of surveys. Yet careful attention to the inclusion of key controls and mediating
processes during the design stage can provide substantial payback during the review process.
Proper inclusion of control variables. The inclusion of appropriate controls allows researchers
to draw more definitive conclusions from their
studies. Research can err on the side of too few or
too many controls. Control variables should meet
three conditions for inclusion in a study (Becker,
2005; James, 1980). First, there is a strong expectation that the variable be correlated with the dependent variable owing to a clear theoretical tie or
prior empirical research. Second, there is a strong
expectation that the control variable be correlated
with the hypothesized independent variable(s).
659
Third, there is a logical reason that the control
variable is not a more central variable in the study,
either a hypothesized one or a mediator. If a variable meeting these three conditions is excluded
from the study, the results may suffer from omitted
variable bias. However, if control variables are included that don’t meet these three tests, they may
hamper the study by unnecessarily soaking up degrees of freedom or bias the findings related to the
hypothesized variables (increasing either type I or
type II error) (Becker, 2005). Thus, researchers
should think carefully about the controls they include— being sure to include proper controls but
excluding superfluous ones.
Operationalizing mediators. A unique characteristic of articles in AMJ is that they are expected
to test, build, or extend theory, which often takes
the form of explaining why a set of variables are
related. But theory alone isn’t enough; it is also
important that mediating processes be tested empirically. The question of when mediators should
be included in a model (and which mediators)
needs to be addressed in the design stage. When an
area of inquiry is new, the focus may be on establishing a causal link between two variables. But,
once an association has been established, it becomes critical for researchers to clearly describe
and measure the process by which variable A affects variable B. As an area of inquiry becomes
more mature, multiple mediators may need to be
included. For example, one strength of the transformational leadership literature is that many mediating processes have been studied (e.g., LMX
[Kark, Shamir, & Chen, 2003; Pillai, Schriesheim, &
Williams, 1999; Wang, Law, Hackett, Wang, &
Chen, 2005]), but a weakness of this literature is
that most of these mediators, even when they are
conceptually related to each other, are studied in
isolation. Typically, each is treated as if it is the
unique process by which managerial actions influence employee attitudes and behavior, and other
known mediators are not considered. Failing to
assess known, and conceptually related mediators,
makes it difficult for authors to convince reviewers
that their contribution is a novel one.
Conclusion
Although research methodologies evolve over
time, there has been little change in the fundamental principles of good research design: match your
design to your question, match construct definition
with operationalization, carefully specify your
model, use measures with established construct validity or provide such evidence, choose samples
and procedures that are appropriate to your unique
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research question. The core problem with AMJ submissions rejected for design problems is not that
they were well-designed studies that ran into problems during execution (though this undoubtedly
happens); it is that the researchers made too many
compromises at the design stage. Whether a researcher depends on existing databases, actively
collects data in organizations, or conducts experimental research, compromises are a reality of the
research process. The challenge is to not compromise too much (Kulka, 1981).
A pragmatic approach to research design starts
with the assumption that most single-study designs
are flawed in some way (with respect to validity).
The best approach, then, to a strong research design
may not lie in eliminating threats to validity
(though they can certainly be reduced during the
design process), but rather in conducting a series of
studies. Each study in a series will have its own
flaws, but together the studies may allow for stronger inferences and more generalizable results than
would any single study on its own. In our view,
multiple study and multiple sample designs are
vastly underutilized in the organizational sciences
and in AMJ submissions. We encourage researchers
to consider the use of multiple studies or samples,
each addressing flaws in the other. This can be
done by combining field studies with laboratory
experiments (e.g., Grant & Berry, 2011), or by testing multiple industry data sets to assess the robustness of findings (e.g., Beck, Bruderl, & Woywode,
2008). As noted in AMJ’s “Information for Contributors,” it is acceptable for multiple study manuscripts to exceed the 40-page guideline.
A large percentage of manuscripts submitted to
AMJ that are either never sent out for review or that
fare poorly in the review process (i.e., all three reviewers recommend rejection) have flawed designs,
but manuscripts published in AMJ are not perfect.
They sometimes have designs that cannot fully answer their underlying questions, sometimes use
poorly validated measures, and sometimes have misspecified models. Addressing all possible threats to
validity in each and every study would be impossibly
complicated, and empirical research might never get
conducted (Kulka, 1981). But honestly assessing
threats to validity during the design stage of a research effort and taking steps to minimize them—
either via improving a single study or conducting
multiple studies—will substantially improve the potential for an ultimately positive outcome.
Joyce E. Bono
University of Florida
Gerry McNamara
Michigan State University
August
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or deceleration? Theoretical and methodological reflections on the analysis of organizational change.
Academy of Management Journal, 51: 413– 435.
Becker, T. E. 2005. Potential problems in the statistical
control of variables in organizational research: A
qualitative analysis with recommendations. Organizational Research Methods, 8: 274 –289.
Block, J. 1995. A contrarian view of the five-factor approach to personality description. Psychological
Bulletin, 117: 187–215.
Conway, J. M., & Lance, C. E. 2010. What reviewers
should expect from authors regarding common
method bias in organizational research. Journal of
Business and Psychology, 25: 325–334.
Devers, C. E., Wiseman, R. M., & Holmes, R. M. 2007. The
effects of endowment and loss aversion in managerial stock option valuation. Academy of Management Journal, 50: 191–208.
Grant, A. M., & Berry, J. W. 2011. The necessity of others
is the mother of invention: Intrinsic and prosocial
motivations, perspective taking, and creativity.
Academy of Management Journal, 54: 73–96.
James, L. R. 1980. The unmeasured variables problem in
path analysis. Journal of Applied Psychology, 65:
415– 421.
Kark, R., Shamir, B., & Chen, G. 2003. The two faces of
transformational leadership: Empowerment and dependency. Journal of Applied Psychology, 88: 246 –
255.
Kulka, R. A. 1981. Idiosyncrasy and circumstance. American Behavioral Scientist, 25: 153–178.
McGrath, J. E. 1981. Introduction. American Behavioral
Scientist, 25: 127–130.
Nyberg, A. J., Fulmer, I. S., Gerhart, B., & Carpenter, M. A.
2010. Agency theory revisited: CEO return and
shareholder interest alignment. Academy of Management Journal, 53: 1029 –1049.
Pillai, R., Schriesheim, C. A., & Williams, E. S. 1999. Fairness perceptions and trust as mediators for transformational and transactional leadership: A two-sample
study. Journal of Management, 25: 897–933.
Podsakoff, P. M., MacKenzie, S. B., & Podsakoff, N. 2003.
Common method biases in behavioral research: A
critical review of the literature and recommended
remedies. Journal of Applied Psychology, 25: 879 –
903.
Wang, H., Law, K. S., Hackett, R. D., Wang, D., & Chen,
Z. X. 2005. Leader-member exchange as a mediator
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娀 Academy of Management Journal
2012, Vol. 55, No. 1, 8–12.
http://dx.doi.org/10.5465/amj.2012.4001
FROM THE EDITORS
PUBLISHING IN AMJ—PART 5:
CRAFTING THE METHODS AND RESULTS
Editor’s Note:
This editorial continues a seven-part series, “Publishing in AMJ,” in which the editors give suggestions and advice for
improving the quality of submissions to the Journal. The series offers “bumper to bumper” coverage, with installments
ranging from topic choice to crafting a Discussion section. The series will continue in April with “Part 6: Discussing
the Implications.” – J.A.C.
Once the arduous, but exciting, work of selecting
an intriguing and appropriate topic, designing and
executing a sound data collection, crafting a compelling “hook,” and developing a solid theory is
finished, it is tempting to sit back, relax, and cruise
through the Methods and Results. It seems straightforward, and perhaps a little mundane, to report to
the readers (1) how and why the data were obtained; (2) how the data were analyzed and what
was found. Indeed, it is unlikely that many readers
of AMJ have waited with bated breath for an entertaining narrative in this installment of the Publishing in AMJ editorial series. If we fall short of being
compelling, therefore, we hope to at least be
informative.
As authors ourselves, we have, admittedly, succumbed to the temptation of relaxing our concentration when it is time to write these sections. We
have heard colleagues say that they pass off these
sections to junior members of their research teams
to “get their feet wet” in manuscript crafting, as
though these sections were of less importance than
the opening, hypothesis development, and Discussion sections. Perhaps this is so. But as members of
the current editorial team for the past two years, we
have come face-to-face with the reality that the
Methods and Results sections, if not the most critical, often play a major role in how reviewers evaluate a manuscript. Instead of providing a clear,
detailed account of the data collection procedures
and findings, these sections often leave reviewers
perplexed and raise more questions than they answer about the research procedures and findings
that the authors used. In contrast, an effective presentation can have a crucial impact on the extent to
which authors can convince their audiences that
their theoretical arguments (or parts of them) are
supported. High-quality Methods and Results sections also send positive signals about the conscientiousness of the author(s). Knowing that they were
careful and rigorous in their preparation of these
sections may make a difference for reviewers debating whether to recommend a rejection or a revision request.
To better understand the common concerns
raised by reviewers, we evaluated each of our decision letters for rejected manuscripts to this point
in our term. We found several issues arose much
more frequently in rejected manuscripts than they
did in manuscripts for which revisions were requested. The results of our evaluation, if not surprising, revealed a remarkably consistent set of
major concerns for both sections, which we summarize as “the three C’s”: completeness, clarity,
and credibility.
THE METHODS
Completeness
In the review of our decision letters, perhaps the
most common theme related to Methods sections
was that the authors failed to provide a complete
description of the ways they obtained the data, the
operationalizations of the constructs that they
used, and the types of analyses that they conducted. When authors have collected their data—a
primary data collection—it is important for them to
explain in detail not only what happened, but why
they made certain decisions. A good example is
found in Bommer, Dierdorff, and Rubin’s (2007)
study of group-level citizenship behaviors and job
performance. We learn in their Methods how the
participants were contacted (i.e., on site, by the
study’s first author), how the data were obtained
(i.e., in an on-site training room, from groups of
20 –30 employees), what kinds of encouragement
for participation were used (i.e., letters from both
the company president and the researchers), and
who reported the information for different constructs in the model (i.e., employees, supervisors,
8
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written permission. Users may print, download, or email articles for individual use only.
2012
Zhang and Shaw
and managers of the supervisors). In addition, these
authors reported other relevant pieces of information about their data collection. For example, they
noted that employees and their supervisors were
never scheduled to complete their questionnaires
in the same room together. In addition, they reported a system of “checks and balances” to make
sure supervisors reported performance for all of
their direct reports. Providing these details, in addition to a full description of the characteristics of
the analysis sample at the individual and team
levels, allows reviewers to evaluate the strengths
and weaknesses of a research design. Although it is
reasonable to highlight the strengths of one’s research, reporting sufficient details on the strengths
and potential weaknesses of the data collection is
preferred over an approach that conceals important
details, because certain compromises or flaws can
also yield advantages. Consider the example of data
collected with a snowball sampling approach in
two waves separated by a few months. A disadvantage of this approach would likely be that the sample matched over the two waves will be smaller
than the sample resulting if the researchers only
contact wave 1 participants to participate in wave
2. But, this approach also has certain advantages. In
particular, large numbers of one-wave participants
(i.e., those that participated either in the first wave
or the second wave) can be used to address response bias and representativeness issues
straightforwardly.
In many other cases, the data for a study were
obtained from archival sources. Here a researcher
may not have access to all the nitty-gritty details of
the data collection procedures, but completeness in
reporting is no less important. Most, if not all,
archival data sets come with technical reports or
usage manuals that provide a good deal of detail.
Armed with these, the researcher can attempt to
replicate the detail of the data collection procedures and measures that is found in primary data
collections. For a good example, using the National
Longitudinal Survey and Youth Cohort (NLSY79),
see Lee, Gerhart, Weller, and Trevor (2008). For
other archival data collections, authors construct
the dataset themselves, perhaps by coding corporate filings, media accounts, or building variables
from other sources. In these cases, a complete description of how they identified the sample, how
many observations were lost for different reasons,
how they conducted the coding, and what judgment calls were made are necessary.
Regardless of the type of data set a researcher has
used, the goals in this section are the same. First,
authors should disclose the hows, whats, and whys
of the research procedures. Including an Appendix
9
with a full list of measures (and items, where appropriate), for example, is often a nice touch. Second, completeness allows readers to evaluate the
advantages and disadvantages of the approach
taken, which on balance, creates a more positive
impression of the study. Third, a primary goal of
the Methods section should be to provide sufficient
information that someone could replicate the study
and get the same results, if they used exactly the
same procedure and data. After reading the Methods section, readers should have confidence that
they could replicate the primary data collection or
compile the same archival database that the authors
are reporting.
Clarity
Far too often, authors fail to clearly explain what
they have done. Although there are many potential
examples, a typical, very common, problem concerns descriptions of measures. Reviewers are often
concerned with language such as “we adapted
items” or “we used items from several sources.”
Indeed, not reporting how measures were adapted
was the modal issue related to measurement in the
evaluation of our decision letters. Ideally, authors
can avoid these problems simply by using the full,
validated measures of constructs when they are
available. When this is not possible, it is imperative
to provide a justification for the modifications and,
ideally, to provide additional, empirical validation
of the altered measures. If this information is not
initially included, reviewers will invariably ask for
it; providing the information up front improves the
chances of a revision request.
Another very common clarity issue concerns the
justification for variable coding. Coding decisions
are made in nearly every quantitative study, but are
perhaps most frequently seen in research involving
archival data sets, experimental designs, and assignment of numerical codes based on qualitative
responses. For example, Ferrier (2001) used structured content analysis to code news headlines for
measures of competitive attacks. In an excellent
example of clarity, Ferrier described in an organized fashion and with straightforward language
how the research team made the coding decisions
for each dimension and how these decisions resulted in operationalizations that matched the constitutive definitions of the competitive attack
dimensions.
Credibility
Authors can do several uncomplicated things to
enhance perceptions of credibility in their Methods
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Academy of Management Journal
sections. First, it is important to address why a
particular sample was chosen. Reviewers often
question why a particular sample was used, especially when it is not immediately obvious why the
phenomenon of interest is important in the setting
used. For example, in Tangirala and Ramanujam’s
study of voice, personal control, and organizational
identification, the authors opened the Methods by
describing why they chose to sample front-line hospital nurses to test their hypotheses, noting (1)
“they are well positioned to observe early signs of
unsafe conditions in patient care and bring them to
the attention of the hospital” and (2) “there is a
growing recognition that the willingness of nurses
to speak up about problems in care delivery is
critical for improving patient safety and reducing
avoidable medical errors (such as administration of
the wrong drug), a leading cause of patient injury
and death in the United States” (2008: 1,193). Second, it is always good practice to summarize the
conceptual definition of a construct before describing the measure used for it. This not only makes it
easier for readers—they don’t have to flip back and
forth in the paper to find the constitutive definitions— but when done well will lessen reader concerns about whether the theory a paper presents
matches the tests that were conducted. Third, it is
always important to explain why a particular operationalization was used. For example, organizational performance has numerous dimensions.
Some may be relevant to the hypotheses at hand,
and others are not. We have often seen authors
“surprise” reviewers by introducing certain dimensions with no justification. In cases in which alternative measures are available, authors should report what
