Topic Choosing a research topic either non-dissertation or by gdf57j

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									Dear graduate students,

The AERA Division D Graduate Student Committee is pleased to announce many news, events,
and beneficial services for you. At the 2008 Annual Meeting, the committee members
formulated an action plan to provide more opportunities for and services to graduate students in
Division D. As a part of the new Division D Graduate Student section of the website, the
committee members decided to launch an "ASK A SCHOLAR SECTION," which is a sequence
of topics that will be discussed by diverse experts in the field of research and methodology.
Comprehensive series of advice related with these topics will be posted every month in our web
site. Our first topic is 'choosing a research topic, either non-dissertation or dissertation.' We are
grateful to Dr. Linda Cook and Dr. Joanna S. Gorin for sharing their thoughts on this topic with
the Division D graduate students. They both provided very rich and rigorous responses in our
structured interview. Dr. Linda Cook is the present Vice-President of our division, and she
works in the research division in Educational Testing Service as a principal research scientist.
Dr. Joanna S. Gorin is an assistant professor at Arizona State University in the division of
psychology in education at measurement, statistics, and methodological studies program. We are
delighted for their participation and support, and we are very confident that their help will benefit
all of us as graduate students. Please revisit our website for our next topic.

Topic: Choosing a research topic either non-dissertation or
dissertation




                                               Dr. Linda Cook

                                               Division D Vice-President

                                               Principal Research Scientist, ETS




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    a) Does it have to be novel, original, broad or specific?


My experience has been that it is very difficult to carry out research on a broad topic. During my
career, I have been approached a number of times by clients who are interested in having
research done in a particular area, but the description of the research that they are interested in
having carried out is sometimes broad and lacking in specifics. A challenge that I have always
enjoyed, when placed in this situation, is to try to get a client to think more specifically about
what they are really interested in finding out. Some of the questions I ask them are: Why are you
interested in having this research done? How do you expect to use the outcomes of the research?
What questions do you expect the research to answer? So, although I think a research topic may
start with a broad statement of the problem, before a research study can actually be designed, it is
always necessary to list the specific set of questions that the study, or program of research, will
address. As far as originality or novelty is concerned, I think it is important not to reinvent the
wheel, but I also think it is important not to choose a topic simply because it seems to be original
or novel. Prior to investing resources in any research project, it is important to consider what
contributions the research will make to a particular body of knowledge. I think, sometimes, in an
effort to provide results that are novel or original, the researcher can loose sight of the fact that
the results of the research should provide useful information that contributes to the general body
of knowledge about the topic. An original or novel solution to a problem may not necessarily
provide the most useful information about the topic.



    b) Should the students be pragmatic in choosing their topic? Does the topic create
       possible job opportunities? For example, should part-time students investigate job
       related dissertation topics? What are the advantages and disadvantages of this idea?


I think it is of primary importance that a student chooses a topic that he or she is interested in and
that is of interest to his/her dissertation advisor. Effective researchers often develop a program of
research early in their careers that they pursue for an extended period of time; a well carried out
dissertation study can provide the basis or beginning for such a program of research.



I believe a dissertation topic should be one that is doable within a reasonable time period with a
reasonable amount of resources. In addition, I think it is also important that a student’s
dissertation topic be sufficiently challenging to provide a rigorous learning experience. Because
a student’s dissertation topic will also serve as a demonstration to future employers that he or she
has developed in depth expertise in the particular area, some topics may be more appealing to
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some employers than others, depending on the specific job opening the employer is trying to fill.
However, attempting to match a choice of dissertation to potential openings in a job market is a
difficult thing to do. Occasionally, an employer is looking for someone with skills in a very
specific area, for example, assessing students with disabilities, and will look for a very specific
background in this area. Generally, employers are looking for a demonstration of a strong
background with in- depth knowledge in an area that is important for the type of work the
institution carries out.



    c) How early or late should students start choosing their research topic? For example,
       how can a student generate emerging ideas for a research topic?


I don’t think it is ever too early for a student to begin thinking about potential research topics.
Typical ways to generate emerging ideas for research studies are to read the literature, attend
conferences, and talk to experts in the field. Another way to generate a meaningful research topic
is to actually begin doing research in the area that is being considered; the results of some small
studies in the area of interest could help provide a foundation for a student’s dissertation
proposal. Finally, I think graduate students should expect to receive advice about potential
research topics from their advisors early on, and frequently, during their graduate student careers.



    d) What are the key points for turning an issue into research questions? What if a
       student wants to replicate an existing study? What are the pros and cons for this
       idea?


I think I have already covered many of the key points associated with turning an issue into
research questions when I addressed the first topic in this interview. I think it is important to ask
who is interested in the issue, who will be interested in the results of research on the topic and
how the results will be used. It is also important to consider whether or not the issue is
tractable—is it amenable to research that can be carried out in a reasonable length of time with a
reasonable amount of resources? When considering whether or not to replicate a study, I think it
is important to ask: What is the purpose of replicating the study? Will the results of the
replication be meaningful and publishable? Will the results contribute to the general body of
knowledge about the topic? That said, I think there would need to be a compelling reason for a
student to choose to replicate a study as a dissertation topic. There is always the risk that the
topic will be seen as less important because the original idea is not one that can be solely
attributed to the student.


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                             Dr. Joanna S. Gorin

                             Assistant Professor
                             Measurement, Statistics, and Methodological Studies Program
                             Division of Psychology in Education
                             Arizona State University




a) Does it have to be novel, original, broad or specific? And b) Should the students be
pragmatic in choosing their topic? Does the topic create possible job opportunities? For
example, should part-time students investigate job related dissertation topics? What are
the advantages and disadvantages of this idea?

Selecting and defining a dissertation topic is one of the most difficult tasks in graduate school. I
think that the only way it comes easily is if you have been involved in as many different research
projects as possible leading up to the dissertation. As for recommendations for topics, I don’t
think that there is a single right answer to this question. I believe strongly that the study itself
must address a specific question, otherwise the student risks never completing the project.
However, this should always be within the context of a broader issue that is of interest to the
educational community. I think that answering a question for which there is no practical
significance may constitute interesting research to the student, but broader interest from those in
the field will be limited. If the topic happens to be novel, that is often beneficial, but I don’t think
that it is a requirement. I know that faculty directing dissertations differ in their views of the
purpose of a dissertation. Some believe that it is simply a means to an end. In this regard, they
encourage students to pick a topic of some interest, formulate a manageable project, and
complete it. Once it’s done, the student will then have the freedom to change their interests and
pursue some other line of research. I do not fall in this camp. In fact, I walked away from a
dissertation topic when I was ABD to pursue and different area of emphasis in psychometrics,
simply because I wanted to complete a dissertation on a topic that sparked my interests more
strongly. Three years later I completed a dissertation on a topic that I continue to research today.
I cannot envision that I would have been able to pursue this line of research if I had not selected
the topic for my dissertation. It has formed the foundation for all of my subsequent work and my
reputation as a researcher in the field of cognitive-psychometrics.



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c) How early or late should students start choosing their research topic? For example,
how can a student generate emerging ideas for a research topic? AND d) What are the key
points for turning an issue into research questions? What if a student wants to replicate an
existing study? What are the pros and cons for this idea?

The best ways to generate ideas for a research topic are to a) read as much of the research as
possible, b) engage in as much research as possible (paid or not), and c) talk to your colleagues
and faculty about your ideas and questions. I would not recommend selecting a topic too early in
a program for several reasons. First, it is unlikely that one is familiar with the existing research
without sufficient time to review the literature. Further, without some research experience in the
area, it is difficult to understand the appropriate scope for a research project. I have worked with
students who are great at generating broad, interesting questions. However, when it comes to
developing a focused research hypothesis or methodology to address the question, they simply
lack the experience because they have not been involved in enough research to understand the
process. Likewise, I have encountered students who think very methodically and understand the
existing psychometric tools, but they lack an understanding of the important issues in the field
today. The best approach to developing a topic could be thought of like focusing a camera. One
needs to move back and forth from a broad view to a focused view iteratively to make sure that
the question has practical significance and is methodologically approachable.




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