Electronic Textbook - "So...What's Your Problem?"

That will be the focus of this chapter. In a way, it's sort of a "prequel" to our work on problem statements in Intro to Research. As dissertation candidates and thus apprentice researchers, you will need to do some solid "upfront" thinking about potentially lucrative topics to pursue. Thus, we'll set the stage for that eventual research question by thinking about 'where problem statements come from.'Next, we'll explode some dangerous myths about what research (particularly your own dissertation) should, or shouldn't, be expected to accomplish. Finally, we'll move into how to focus the broader topics of your interest, in order to make them more doable.

Have a look at this web site from Cornell University for a reading on how to choose a research topic.

Cornell-Choosing a Research Topic
Problem Formulation: Where do research topics come from?

I. General Sources for Potential Research Topics: A "Tip Sheet"

1. A practical need to know. This one almost seems self-evident, doesn't it?! Yet we sometimes dismiss it because it "doesn't seem rigorous," "seems too obvious," and so forth. However, I would say exactly the opposite: that a practical need for information is the ultimate reason for doing research! rather than a "hoop jump," "another publication under one's belt," "stats for the sake of stats," etc.!

   
   A few years back, I wrote a paper called Dare to Do Research! It is a straight-talk discussion of how practitioners can, and should, make the best use of so-called stats/computer/research consultants. (I hope you'll want to look this paper up! I think you'd enjoy it! It's been published in ERIC.) Anyway, in this paper, I rather enviously point out that you are in a far better position to "do research" than a numbers-type like me! That's because, in your day-to-day involvement with schools, clinics, educational training programs, etc., you have a closeup view of "what's working," "what isn't," and "who needs to know what."

   
   It is exactly this kind of need or curiosity that impels a scientific investigation to attempt to come up with the answer!

   1. Who needs to know what and why? - > Your Purpose of the Study; and
   2. What is it you are needing to know? - > Problem Statement/Research Question(s)

   
   Prior to presenting her study itself, a recent successful doctoral defendee told us in her opening comments about her work in family counseling and child behavior problems. She then eloquently spoke of a continued problem she encountered when the parents were themselves adult children of alcoholics (ACoA's). In her experience, these ACoA parents consistently seemed to have difficulty learning and putting into practice some basic communication and child-rearing practices with their children. This need to know what it is about ACoA parents that caused them difficulty in parenting their own children impelled her to develop a research topic designed to identify such problems.
   

2. "Inheriting" a database or topic from a faculty mentor or research sponsor. This one can be both a blessing and a curse! On the up side, working side by side with a faculty member who's supervising a research project gives you invaluable inside experience. You are steeped in the topic itself, as well as the daily nuts and bolts of carrying out the research. (Surprise, surprise! often nothing like the ivory-tower textbooks describe ... !) In fact, I remain a firm believer that the best way to learn research is to be thrown into actually doing it!

   
   Another plus is that by being lucky enough to work with a faculty research mentor, you may get to "inherit" either the topic itself, or a spinoff from the database, to work up your own dissertation topic. Kind of takes the heat off having to brainstorm your own idea from scratch!
   

   Ah ... but that too can be the very curse. Having it more or less handed to you can also basically eliminate the "from within," "personal buy-in!" that is often the driving force of your sticking with the thing despite problems and hangups! Will you have the same "burning motivation" to dig into the nuances of it, push past annoying little hangups like a flukey statistical result on a computer run, etc., etc., when it's "not really your thing?!" So, you see, this sometimes works against you in the long run as well.
   

   The ideal, of course, is to have both a) an inherent interest in the topic; and b) ready access to a mentor, database, etc. (Nice if you can get 'em! Now try telling that to financial aid grantors!)
   

3. You pick up where someone else has left off! This solid-gold tip was passed along to me by my own dissertation chair - and what a gem it is!
   
   I think it's especially valuable when you "kind of, sort of" know the general direction of your interests -- yet you don't yet have a focused, crystallized vision of "what, exactly," about that topic you want to pursue. This appears to be the polar opposite of your colleagues in point #1, above, who start with a grass-roots practical need and then will build the rest of the topic, including a supporting structure of literature review, around it.
   
   Let's say you've done some papers and/or presentations for coursework in a general topic area - for example, the effects of peer coaching on teacher performance. You know you are interested in finding out more about this general area but don't yet have a clear road map of what it is you want to investigate about it.
   
   As part of your preparation for your papers or class presentations, you've probably done extensive library literature reviews. In fact, you've probably got stashed away a box or bulging file folder of Xeroxed journal articles, conference papers by others, etc., that you eventually worked into your own paper.
   
   What my adviser recommended to do is this: sort of "re-read 'em backwards!" That is: start at the end, where the authors give "Recommendations" for future research directions. Almost all refereed journal articles and conference handouts end this way. The authors summarize what they did, and then give some "down the road" future projections as to what the logical next step in the research chain might be.
   
   You might find, for instance, that in your "backwards reread" of your literature review sources, some authors have recommended combining peer tutoring with shadowing or classroom observations, and then measuring the joint, synergistic impact of both interventions. Or they might suggest that gender could be a key variable: matching same-gender teacher mentors and protege(e)s and comparing to cross-gender pairings to see if that makes a difference. Or, the authors might add a "tail-end" variable. So we've seen it works for improved teacher performance, they contend. Well, what about other potentially revealing and important outcomes besides teacher performance? like teacher motivation? satisfaction? turnover?

   You pick up where others have left off! As we discussed in EDR 610, Intro to Research, all research, whatever the topic, is in essence a cyclical life cycle. A given investigation ends with a peek at future directions -- exactly where the next step in understanding that topic starts. Rereading others' "future directions" is often quite helpful in giving you ideas as to how to focus your own interests in a broader topic area. Also, we'll see how to directly apply this tip when we explore "adding a variable" to help focus our topics of interest in Part III of this module.
   
   Now on to (hopefully) exploding some related fallacies, about "what isn't," and "what not to do!"
   
   

1. Dissertation research has to be "totally original" research! For this one I want to joyfully cite and thank our Pt. Loma Intermediate Statistics partner, Darlene Bates! Darlene and I got into a great dialogue about this regarding her own topic. As she so astutely pointed out, "Is there anything left that's really totally original anyway?!" And I think she's right!!!
   In some of my past "live and in person" EDR 610, Intro to Research classes, we talked about three very broad "families" or types of research:
   
   
   1. Basic research - This is that never-before-existed and totally esoteric (with no need or concern by the present researcher for practical application at this point in time, at least) research. Think of Einstein deriving reams of equations and you've got the idea. Impressive, to be sure, but how realistic? doable? attainable by even one single 'genius' in his/her lifetime?! A laudable goal for one's lifetime research pursuits -- *not* recommended for a dissertation if you hope for there to be life past the defense (and hard as it may be to believe, you *should!*)!
      
   2. Applied research - This one begins to "get real." In it, you are hoping to apply the "laws of science/nature" to some broader practical field. Think of Maslow's pyramid - broader laws of human learning applied to a model or theory of acquisition of specific learning skills.

      Maslow's Pyramid

      This begins to narrow down into a specific field of interest.
      

   3. Action/evaluation research - The polar opposite of # 1, above. I have a burning, critical need to solve this discipline problem for this child at this school setting - help me make it better! Get me results, and I want those results to emanate from a 'scientific investigation:' e.g., a well-designed and implemented research study to 'cure the problem.' And if the things you find "work" for your situation (e.g., the incidence of behavioral problems does significantly decline) also happen to apply to other settings, places, circumstances -- well, that is gravy! But again, not your own immediate goal for this particular action research study!
      A similar scenario is in place for evaluation research? Did "it" [teaching method, counseling procedure, vocational/technical training program, etc.] 'work?' There are two components to this:
      
      1. Did it "run" as planned? AND
      2. Did it lead to the desired outcomes?
         

      I'd like to use a medical analogy to illustrate that while desirable, (a) and (b) may not necessarily go together and thus are two subtly different components. I may take a prescribed medication as planned (e.g., amount of dosage, spacing of time between successive doses, other directions like not mixing alcohol or certain foods with it). So the answer to "a" is "yes." But despite such 'playing by the rules,' I may either fail to get better and/or experience some negative side effects - either anticipated or unanticipated. So at the same time, the answer to "b" is "no." The desired outcome of "recovery from illness/good health" was not attained, and at the same time some negative outcomes (side effects that make me sicker) do crop up. So, that necessitates a reassessment of the 'intervention'. The physician and I would look at what has happened, and he/she may decide to go to a different drug, tinker with the dosage of the present drug, or other similar measures to get it to work better. So too it is with the evaluation scenario. Following the plan to the letter (a) is expected to, but doesn't always, produce the predicted target outcomes (b). If this happens, the evaluation findings would imply reassessing the intervention (teaching method, teacher recruitment/retention incentive plan, counseling method for clinically depressed teenaged women, etc.) and modifying some, or all, of it as a reult.
      

      A long digression, hopefully of interest! since as you may know, evaluation research happens to be one of my specialties ... ! But hopefully you get the point.
      

      Back to the listing of three broad classes or families of research, again my goal was to try and convince you that "pure originality" is rare and not likely to be very practicable for a given research study - let alone a dissertation that you hope to complete in a lifetime!
      
      
   I'd venture to say that most "doable and yet reasonably rigorous" studies will fall between "2 1/2 and close to 3," in this preceding list! You wouldn't want to commit to doing all of the "applying" to a given field (purist, extreme version of # 2). We'll talk more about that in a bit with regard to "carving out a reasonable focus" for your study! At the same time, while it's good to have the need emanate from a practical problem (and we saw this in Tip # 1 for sources of ideas), it is desirable for you to at least "somewhat care about" the issue of generalizability of your findings and results. At the very least, you will need to be aware that this is an issue when your own individual study is placed in the broader context of all research in that one given area (e.g., parenting skills of ACoA's). What would you then advise someone else who would like to "take off" on your one individual study?
   

   Bottom line time: Don't think you have to reinvent the world! Care more about a substantive, focused problem and the scientific methods and procedures you're supposed to apply to it! Demonstrating your ability to pursue a researchable question using such scientific procedures is what will be evaluated in terms of your dissertation -- as opposed to "never-before," wildly creative, earth-shattering new idea!!!
   

2. Closely related: A replication study "doesn't add enough" to knowledge to "make a good dissertation topic!" Somehow, this one feels like "cheating," or "getting off too easy" to students!
   

   Yet think about a "scientific law" that you learned when you first studied what a "theory" was. It in you were (hopefully!) told that a theory is our "best web of explanatory variables" thus far about a given phenomenon." What leads to what? Is there a difference in "it" (motivation, satisfaction,etc.) by gender? years of experience? What has a positive impact? negative impact? And in turn, what does the motivation or satisfaction influence? We chain together these pre- , differencing and post- variables to put together our best understanding or explanation to date of this broader construct, "motivation." That's our theory.
   

   You probably (hopefully?) learned that 'strictly speaking, a theory can never be 'absolutely proven.' That's where replication studies come in. You can try to literally recreate the conditions and circumstances of a past study and see if you also then can reproduce the same findings, results and conclusions. Will peer-assisted coaching, done the same way, same number of visitations, same subject area, same level of grade taught, as in Study X yield the same positive outcomes? If so, you have literally replicated the conditions of the study. If you do find the same results, then your finding is basically, "Yes, the theoretical relationship between this peer coaching and teacher performance appears to hold up." And so the theoretical explanation stands -- for now, at least.
   

   And although you might not have realized it, strictly speaking, you did alter at least one key variable -- regardless of how careful you were to randomize, match, literally reproduce, as many of the original circumstances and conditions as possible. That variable is time! By redoing the study exactly, even if you happen to be in the exact same location, you are doing it again -- and thus seeing if the original hypothesized relationships among the key variables "manage to hold up" since the time that they were initially investigated. This is a contribution to the research chain/life cycle and therefore to knowledge as a whole about this pheonomenon!
   

   Of course, you could very well find, even with your best attempt at a strictly literal replication, that your outcomes turn out to be totally different from those of the original study! It happens -- especially as we get away from such strictly controlled, purist-type of experimental designs. So -- now it becomes interesting and more substantive (messier, perhaps?!)! You've got some explaining to do! And that is where those additional potential variables come in -- what else could have intervened? accounted for the difference? So this too will add to our eventual knowledge -- if only in the form of your own recommendations on how future investigations should be altered to take some of these add'l. variables into account! So here again, your replication added to our existing body of knowledge via unearthing surprise findings and suggesting future directions for research to attempt to explain or reconcile those findings!
   

   Again, sharing the advice of my own dissertation chair here: if you are truly worried that your literal replication "won't be enough," I'd say to combine this replication with Tip # 3: replicate and extend! This would be like a two-phase investigation. After you attempt to reproduce the original findings, then add in a potential explanatory variable or two (perhaps suggested by prior researchers in this area -- or even better, follow your own hunches!) and see what that does to the original hypothesized relationships!
   

3. I have to "do a WHOLE LOT" to produce a substantive, defensible dissertation! This too seems to be the polar opposite of # 2, above, and is kind of implied by the "originality myth," # 1 fallacy, in our preceding discussion.
   

   It is also a danger if you're "too personally steeped/involved in" your own research! Guess I'm saying that "burning desire and passion" for your research is a plus in keeping you going over the rough spots. At the same time, it can become a detriment if you basically 'don't know when to quit.'
   
   You end up carving out too wide a path for yourself (with your proposed dissertation study constituting, in essence, several dissertations -- now, you really don't have to have 5 Ed.D,'s, do you???!!!). Our Part III, where we look at the "add-a-variable" method, is a really good self-exercise for you to try and do if you (or, hopefully, your protective chair -- I'm like that and so was my own!) think that you've bitten off more that's fair for you to chew for a doctoral dissertation.
   
   Remember -- from your previous reading(link to Chapter 1 of ET)-- there's a good place to put all that you didn't or couldn't do, but still want to prove that you've thought deeply about! That would be Chapter 5! Especially your own recommendations for future research!!!
   
   Bottom line time: Carve out a manageable chunk - do it - and then provide your scholarly recommendation for including all of the rest in Chapter 5's future research recommendations!
   
   

4. It has to be perfect in every way to be "good" research! Ah ... the reason for being of 12-step and other self-esteem/personal-empowerment programs -- let alone the dissertation!!
   
   There's NO such animal as a "PERFECT research study!"
   
   Remember "Limitations?!" We'll revisit that issue. But Limitations, which we put in Chapter One, constitute the "threats to validity," or possible alternative, competing explanations for why you found what you found!
   
   Even in the most tightly controlled true experimental-type study, there are many, many choices to be made and therefore, subtle biases ALREADY BUILT IN! Why this treatment? for this length of time? with this age of subject? and not some others? and so on and so forth! Just because you're tightly controlling those variables, doesn't mean they're the only, or major, reasons for why you found what you found! and that some other variables wouldn't have "worked better!"
   
   And, of course, the potential for such "rival explanations" becomes even greater, the farther away we move from this (rather unrealistic to begin with) true experimental model. For the "reality-based, field-based," practical hands-on research that we as educators do in real settings, with real people, we may need to go non-experimental in our designs to begin with.
   
   But just because such threats to validity exist -- as they do for all types of designs -- that doesn't mean our research isn't "good!" There are many things we can do to ensure top quality in all phases of our design and procedures. These include, for instance, pilot-testing our instrumentation to help ensure reasonably high levels of its validity and reliability. Another is in the sampling plan that we use to select our subjects. These factors, then, are assessed to determine the quality of our research -- as opposed to the unattainable "perfection." Specifically, the readers and evaluators of your research (for now: read, "chair and committee"!) will be looking for two things:
   
   
   1. Did you indeed follow "high quality" principles in all phases of your design and analysis - e.g., pilot testing your instrumentation?
      
   2. Are you aware of some potential threats to validity (rival, competing explanations for why else you may have found what you found), and have you alerted the reader to these in your Chapter One Limitations discussion?
      
   
   
5. A 'good' dissertation topic needs to emanate from my all-consuming passion for a given topic. We've alluded to the pluses of this one: if you care deeply, it will keep you going through the inevitable 'rough spots' that are part and parcel of actually rolling up your sleeves and doing your research -- e.g., the disappointment when you don't get back at least 70% of your surveys on your first try, and you have to step back and reprod your subjects with a reminder letter. Certainly, you are far less likely to get discouraged, give up in frustration, etc., if the topic is one that interests you deeply. The down side is possibly carving out too broad a niche and/or tinkering past the point of when it is ready in a misguided drive for perfection.
   
   Yet another potential danger is this: especially when this topic is controversial, 'sexy,' or somehow the center of your existence, you may slip into bringing some subtle biases into your research process. In your mind, you may already have decided how you "need" or "want" those results to turn out. In the many hats I wear, I too, have to be careful here. As many of you know, I've actively done research in the area of diabetes. *Of course* I want that cure to be found! On the other hand, if I am following "scientific procedures of investigation" which are the hallmark of the research process, I should be prepared for the fact that the answer to a research question could very well be "no." And that is what I must be prepared to live with, disappointed though I may be!
   
   This is not to suggest that there is no place for your own "passion" regarding the topic. There is: as a matter of fact, an entire chapter of your dissertation, Chapter Five! In your Implications, you are expected to bring zeal, feeling and passion when you tell the world how it has become a better place (WHO is BETTER OFF and HOW) as a result of your choosing to undertake your research study! You are also expected to point out 'surprise findings,' 'disappointing results,' etc., and candidly speculate on why things might have happened as they did. What else could you, or someone else, have done differently? Could some other ways be tried in the next replication and extension of this particular research?
   
   Clearly, these are different from subtly "pre-biasing" your research questions, though. If you sense that your research questions are not really "open-ended," that is, that you've subtly predetemined how things "should" or "need to" turn out, it may be a danger signal that you are perhaps too overinvolved with this particular topic to be able to be scientifically objective about it.
   

1. You "start broad" with the general topic of your interest.
   
   
2. Then you try and identify other variables or factors that might relate to your central variable of focus.
   
   Before you know it, you've built a chain reaction of potential relationships, moderating variables, outcomes, and the like. These are not only helpful in understanding your major topic (central variable); by building some of them into your study, you will effectively be narrowing its focus and making it more doable.
   

Now: thats a broad area all right! And in fact if you are interested doing purely exploratory descriptive study would indeed pose research question such as: "What the major perceptions of elderly as seen by younger adults?" or something similar. In fact, to jump fence into our other fall research class, qualitative, for moment: simply leaving it in that broad, blank-slate form not pre-specifying some categories factors, you'd be allowing answers to "emerge," in classic "grounded-theory" style from your interviews, open-ended survey responses or other qualitative data sources. Again, this is OK, particularly when we dont have a lot of prior theory or other type of knowledge to go on and are needing start from "ground zero."

But, for most actual topics of interest to us as educational researchers, we can do a bit better than that! Even for exploratory work, it doesn't hurt to specify some parameters or focal points of interest. We can do that and still let the responses emerge within those boundaries.

For example, back to our area of interest of the perceptions of the elderly, suppose that we focused our research question as follows: "What is the role of the media in shaping young adults' perceptions of the elderly?" Then we've bounded the study by adding the preceding variable:

The addition of this variable adds focus not only to our original research question, but to the resulting methodology and analysis used to address it. If we are planning interviews, for instance, we will only structure our questioning around the media as it impacts the young adults' perceptions. Or, to use yet another qualitative example, we may elect to do content analysis of key newspaper articles, TV shows, films, and so forth regarding the images they engender of senior citizens.

The list of such "bounding" or delimiting moderating variables is virtually endless.

Suppose we had chosen this 2nd-stage brainstorming focus: "What is the role of legislation in shaping social perceptions of the elderly as seen by young adults with an elderly parent living in the home?"

Then we would have two such variables:

Please note that a variety of direct and indirect effects is possible, particularly as we add more and more moderating/mediating variables to our "mini-theory" of relationships. The legislation could directly affect the perceptions. Or, it could also result in an indirect effect by, say, offering incentives for choosing to have semi-invalid parents living in one's adult home, as opposed to choosing nursing home facilities. And finally, there is a possibility of a "feedback loop," in which the perceptions held of the elderly influence the type of legislation that is produced by the young-adult legislators which impacts these elderly citizens' lives. Each of these paths, in turn, implies a separate, distinct, research question or sub problem.

A second, complex and yet focused, example comes from the research of Patterson, DeBaryshe, and Ramsey (1989). They have been developing and refining a theoretical model to explain deviant aggressive behavior in young adult males. Their model causally links such factors as parental discipline and role modeling to the incidence of aggressive actions. However, there is also a middle level of effect: the type and quality of interaction between the child and his peers during the early school years. This middle level is influenced by the earliest parental modeling. It subsequently also impacts upon the incidence of aggressive behavior in the teen years.

This, then, is the general idea. You would start with your central focus and then "flesh out some paths" of related variables or factors:

1. antecedent/pre: causal/influential; precede the desired central focus in some manner (e.g, time);
   
2. mediating/moderating: may follow the antecedents in "a," result from them and yet also exert their own impact on the desired central focus; and
   
3. outcomes/post: key variables that may result, directly or indirectly, from that main focus of interest. This could include "feedback loops" swinging back to the variables in parts (a) and (b), as we saw in the "perceptions of elderly" - > "legislation" example (e.g., directionality "goes both ways").

This, then, is the general idea! By such adding on of variables to "tell the story" of your main focus of interest, you accomplish several goals:

1. You think more deeply, as well as creatively, about your general area of interest, thus gaining insight into why it interested you in the first place and what, exactly, you would like to understand about it:
   
2. You also focus your study, by building in these boundary variables and thus helping avoid the trap of "going too broadly";
   
3. Related to this, you can thus specify your research questions and sub problems with greater precision. Each "path" between one or more variables depicts a separate relationship (difference, cause/effect situation) to be expressed by way of its own research question. In a nutshell, the variables and their relationships are transformed from the path diagram into words to form the sub problems!

Next time, we'll sharpen our focus still more, by reviewing the material on problem statements from Intro to Research. If you will please take a look at the "doctoral proposal handout" that you received along with the course syllabus, you'll see where this goes in the "scheme of things." As we pointed out, while it is not the first item discussed in the proposal, it is really the "heart and soul" of everything else that precedes and follows it.

To that end, you'll begin to build your own doctoral proposal next time! Specifically, you'll be doing the following:

1. Specifying your problem statement/research question(s)/any and all related sub problems - the WHAT (you will do) of your study;
2. "Front-ending" it with the WHY (Purpose of the Study); and
3. "Rear-ending" it with the SO WHAT (who is expected to be better off and how as a result of your choosing to undertake this study - the Significance of the Study).

Go on to Group Assignment 1: Discuss Myths and Misnomers
or
Go back to Topic 3: So... What's Your Problem?

E-mail M. Dereshiwsky at statcatmd@aol.com
Call M. Dereshiwsky at (520) 523-1892

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