how to choose a research projectChoosing a research project |
CHAPTER 6 |
This chapter provides a set of key decision points of reference on which researchers can reflect and plan. It addresses:
how to choose a research project
the importance of the research
the purposes of the research
ensuring that the research can be conducted
research questions
the scope of the literature review
summary of key issues in choosing a research topic or project
This is the first of two chapters that concern the planning of research. This chapter concerns the selection of the research and the initial, practical matters that researchers will find it helpful to address, whilst Chapter 7 unpacks several of these in greater detail. The reader is advised to take these two chapters together.
This chapter sets out a range of very practical issues that researchers have to face when choosing and deciding the project on which they will be working. It is drawn not only from relevant literature but from our own experiences of supervising several hundred research students. Research is a practical activity, and the advice that we give here is practical. This is not a simplistic recipe or low-level ‘tips for researchers’; rather it is distillation of key features of practicable research that, together, deliver relevant and useful findings.
Choosing a research project is normally the decisive feature of successful research. Many novice students and researchers start with an overambitious project. The task of a mentor or supervisor is to help the novice student or researcher to narrow and hone down the research field in order to render the research practicable, useful and workable. Indeed part of the discipline of choosing and conducting a piece of research is fining it down to manageable/researchable proportions (cf. Hopkins, 1985: 47), to enable rigour (e.g. fitness for purposes and methodological soundness) to be inserted into the research. Rigour in planning and doing research lies in choosing a project that is tightly framed. A research topic is only one small aspect of the field of the subject, and careful boundaries must be drawn around the topic: what it will and will not do.
For novice researchers, a piece of educational research often starts by wanting to be their life story or the opportunity to give their personal opinions some grounding in literature and empirical study that will support their opinions or prejudices. This is not the task of research. The task of research is to find out, to investigate, to develop, to test out (e.g. a theory), to address questions that ask, for example: ‘what if’, ‘how’, ‘why’, ‘how well’, ‘what’ and ‘where’.
Several points can give rise to a research topic. For example, for many teachers it may be a problem that they encounter in their day-to-day work: they may want to find out the causes of the problem and how to solve it; they may want to plan an intervention to see how well it addresses or solves the problem. Examples of these might be: ‘how can teachers improve students’ learning of algebra in lower secondary schools?’; ‘how to maximize the learning of students with Asperger’s syndrome in mainstream schooling?’; ‘how to conduct a music lesson with many musical instruments, without the lesson descending into chaos and noise?’; ‘how to teach speaking of a foreign language in large, mixed-ability classes?’.
Some research projects may begin with an area of interest or personal experience that researchers may have been wanting to investigate, for example: ‘why do boys appear to underachieve in secondary school music?’; ‘what is the long-term effect on employment of early school dropout?’; ‘how effective is early identifi-cation of behaviour disorders on educational provision for such students?’; ‘how can teachers improve students’ motivation to learn a second language?’; ‘why do young teachers leave teaching and older teachers stay?’.
Some research topics may begin with a recognized area of importance or topical concern in the field, for example: ‘how to maximize primary students’ learning using ICT’; ‘what is the effect of frequent testing on students’ stress?’; ‘do screening tests of attainment actually measure attainment?’; ‘how can developments in brain research and cognitive neuroscience impact on pedagogy?’; ‘what is the predictive validity of personality tests or learning style inventories on success of first-time employees’ applications for employment?’; ‘do interactive teaching methods produce higher test scores in university students than lecture-based teaching?’. Such importance may arise from coverage of the topic in the press, articles, conference papers and journals.
Some research is conducted as part of a sponsored research project, in which the field and purposes of the research have to be spelled out very clearly in order for the sponsorship to be obtained (for example in the UK the Economic and Social Research Council (www.esrc. ac.uk/ESRCInfoCentre/index.aspx), and the Leverhulme Trust (www.leverhulme.org.uk/) require detailed applications to be completed, and in the USA the United States National Research Council (http://sites.nationalacademies.org/NRC/index.htm) and the Social Science Research Council (www.ssrc.org) require similarly high levels of detail). Such funding might also need to fit into categories of research areas set out by the funding agencies.
A decision on what to research can arise from several wellsprings:
a problem encountered in researchers’ everyday work or outside their everyday work (e.g. conceptual, theoretical, substantive, practical, methodological);
an issue that the researcher has read about in a journal, book or other media;
a problem that has arisen in the locality, perhaps in response to government policy or practices or to local developments;
an area of the researcher’s own interest;
an area of the researcher’s own experience;
a perceived area of importance;
an interesting question;
a testable guess or hunch;
a topical matter;
disquiet with a particular research finding that one has met in the literature or a piece of policy (e.g. from the school, from a government), and a wish to explore it further;
an awareness that a particular issue or area has been covered only partially or selectively in the literature, and a wish to plug the gap;
a wish to apply a piece of conceptual research to actual practice, or to test a theory in practice;
a wish to rework the conceptual or theoretical frameworks that are often used in a specific area;
a wish to revise or replace the methodologies that are often used in researching a specific area;
a desire to improve practice in a particular area;
a desire to involve participants in research and development;
a desire to test out a particular methodology in research;
an interest in seeing if reported practice (e.g. in the literature) holds true for the researcher’s own context (e.g. a comparative study);
an interest in investigating the causes of a phenomenon or the effects of a particular intervention in the area of the phenomenon;
a wish to address an issue or topic that has been under-researched in the literature;
a priority identified by funding agencies;
an issue identified by the researcher’s supervisor or a project team of which the researcher is a member;
a wish to explore further or to apply an issue or topic that one has encountered, e.g. in the literature.
Moreover, a salutary point for researchers to observe is that the study on which they might embark will probably take weeks, months and maybe years. Sustaining interest and momentum in the researcher(s) are important considerations. Researchers should ask themselves whether they really have the interest in studying the issue in question or in conducting the research for a long period of time. If the answer is ‘no’ then, if they have the luxury of not having to do this particular piece of research, they may wish to consider an alternative area of research that will enable them to sustain interest in, and motivation for, the research. A piece of research that is conducted by an unwilling or bored researcher could easily turn out to be unimpressive.
Whatever research area or topic is identified, it is important for the research to be original, significant, non-trivial, relevant, topical, interesting to a wider audience and to advance the field. For example, I may want to investigate the use of such-and-such a textbook in Business Studies with 16-year-olds in Madagascar, but, really, is this actually a useful, formal research topic – will it actually help or benefit other teachers or educationists, even though it yields original data?
Or I might conduct research that finds that older primary children in a deprived area of Aberdeen, Scotland, prefer to have their lunch between 12 noon and 1.00 p.m. rather than between 1.00 p.m. and 2.00 p.m., but, really, does anybody actually care? The topic is original and, indeed, the data are original, but both are insignificant and maybe not worth knowing.
In both these examples the research brings about original data, but that is all. Research needs to go beyond this, to choose a significant topic that will actually make an important contribution to our understanding and to practice. Originality alone is not enough. Rather, the research should be able to move forward the field, perhaps in only a small-scale, piecemeal, incremental way, but nevertheless to advance it such that, without the research, the field would be poorer. Hence it is important to consider how the research takes the field forwards not only in terms of data, but also conceptually, theoretically, substantively, methodologically. At issue here is not only the contribution to knowledge that the research makes, but the impact of that knowledge, indeed funding agencies typically require an indication of the impact that the research will make on the research community and more widely, and how that impact will be assessed and known. What will be the impact, uptake and effects of the research, and on whom?
Further, it is useful for the researcher to identify what benefit the research will bring, and to whom, as this will help to focus the research and its audience. Fundamentally, the questions are: ‘What is the use of this research?’ ‘What is the point of doing this research?’ ‘Is this research worth doing?’ If the answers to the last question is ‘no’, then maybe the researcher should abandon it, otherwise it ceases to be useful research and becomes an indulgence of the dilettante.
Many novice researchers may not know whether the research is original, significant, important, complex, difficult, topical and so on. Here it is important for such a novice to read around the topic, to conduct a literature search, to conduct an online search, to attend conferences on the topic, to read newspaper reports on the topic, in short, to review the state of the field before coming to a firm decision on whether to pursue research in that field. In this respect, if the researcher is a student, it is vital to discuss the proposed topic with a possible supervisor, to receive expert feedback on the possible topic.
The University of California at Santa Cruz (2010: 1) (http://library.ucsc.edu/help/howto/choose-a-research-topic) notes that, before a researcher takes a final decision on whether to pursue a particular piece of research, it is useful to consider selecting a topic that interests the researcher, read through background materials and information and compile a list of keywords, clarify the main concepts and write the topic as a statement (or a hypothesis). Whilst this is perhaps incomplete, nevertheless it provides a useful starting point for novice researchers contemplating what to research.
Implicit in the previous section is the question ‘why do the research?’. This is ambiguous, as ‘why’ can refer to reasons/causes and purposes, though the two may overlap. Whereas the previous section concerned reasons, this section concerns purposes: what we want the research to achieve.
It is vital that the researcher will know what she or he wants the research to ‘deliver’, i.e. to answer the question ‘what are the “deliverables” in the research?’. In other words, what do we want to know as a result of the research that we did not know before the research commenced? What do we want the research to do? What do we want the research to find out (which is not the same as what we want the results to be: we cannot predict the outcome, as this would be to ‘fix’ the research; rather we state the kind of information or answers we want the research to provide)?
In this respect it is important for the researcher to be very clear on what the purposes of the research are, for example:
to try to demonstrate that such-and-such works under a specified set of conditions or in a particular context (experiment; action research);
to increase understanding and knowledge of learning theories (literature-based research);
to identify common features of successful schools (research synthesis; descriptive research);
to examine the effects of early musical tuition on general intelligence (meta-analysis; multilevel research);
to develop and evaluate community education in rural and dispersed communities (participatory research; evaluative research; action research);
to collect opinions on a particular educational proposal (survey);
to examine teacher–student interactions in a language programme (ethnography; observational research);
to investigate the organizational culture of the science faculty in a university (ethnography; survey);
to identify the relative strengths of a range of speci-fied factors on secondary school student motivations for learning (survey; observational study; multiple regression analysis; structural equation modelling);
to see which of two approaches to teaching music results in the most effective learning (comparative study; experiment; causal research);
to see what happens if a particular intervention in setting homework is introduced (experiment; action research; causal research);
to investigate trends in social networking in foreign language teacher communities (network analysis);
to identify the main ways in which teachers in a large secondary school view the leadership of the senior staff of the school (personal constructs; accounts; survey);
to interrogate government policy on promotion criteria in schools (ideology critique; feminist critique);
to see the effects of assigning each student to a mentor in a university (survey; case study; causal research);
to examine the long-term effects of early student dropout from school (survey; causal or correlational research);
to see if repeating a year at school improves student performance (survey; generalization; causal or correlational research);
to chart the effects of counselling disruptive students in a secondary class (case study; causal or correlational research);
to see which catches richer survey data on student drug usage: questionnaires or face-to-face interviews (testing instrumentation; methodology-related research);
to examine the cues that teachers give to students in question-and-answer classroom episodes (discourse analysis);
to investigate vandalism in schools (covert research; informer-based research);
to investigate whether case studies or surveys are more effective in investigating truancy in primary school (comparative methodology);
to run a role-play exercise on communication between a school principal and senior teachers (role play);
to examine the effects of resource allocations to underperforming schools (ideology critique; case study; survey; causal research);
to understand the dynamics of power in primary classrooms (ethnography; interpretive research);
to investigate the demise of the private school system in such-and-such a town at the end of the nineteenth century (historical research);
to understand the nature of trauma and its treatment, on primary aged children living in violent households (case study; action research; grounded theory; ex post facto research);
to generate a theory of effective use of textbooks in secondary school physics teaching (grounded theory);
to clarify the concept of ‘the stereotype activation effect’ for investigating the effect of sex stereotyping on reading in young teenagers (survey; case study; experiment; causal research);
to test the hypothesis/theory that increasing rewards lose their effect on students over time (experiment; survey; longitudinal research; causal or correlational research).
As can be seen in these examples, different purposes suggest different approaches, so ‘fitness for purpose’ takes on importance in planning research (discussed in the following chapter). One can also see that there is a range of purposes and types of research in education. The researcher cannot simply say that he or she likes questionnaires, or is afraid of numbers, or prefers to conduct interviews, or feels that it is wrong to undertake covert research so no covert research will be done. That is to have the tail wagging the dog. Rather, the research purposes determine what follow in respect of the kind of research, the research questions, the instruments for data collection, the sampling, whether the research is overt or covert (the ethics of research), the scope of the research and so on.
Many novice researchers, with the innocence and optimism of ignorance, may believe that whatever they want to do can actually be done. This is very far from the case. There is often a significant gulf between what researchers want to do and what actually turns out to be what they can do.
A formidable issue to be faced here is one of access. Many new researchers fondly imagine that they will be granted access to schools, teachers, students, parents, difficult children, students receiving therapy, truants, dropouts, high performers, star teachers and so on. This is usually NOT the case: gaining access to people and institutions is one of the most difficult tasks for any empirical researcher, particularly if the research is in any way sensitive. Access problems can prevent the research from starting at all, or they can distort or change the original plans for the research.
It is difficult to overstate the importance of researchers doing their homework before planning the research in any detail, to see if it is actually feasible to gain access to the research sites or people that they want. If the answer is ‘no’ then the research plan either stops or has to be modified. This means that it is not uncommon for the researcher to approach some organizations (schools, colleges, universities, government departments) with some initial, outline plans of the research, to see if there is a possibility, likelihood or little or no chance of doing the research.
Nor is it enough to be clear on access; supplementary to this is ‘access to what?’. It is of little use to be given access to a school by the school principal if the teachers have not been consulted about this, or if they are entirely uncooperative (this relates to the issue of informed consent, discussed in Chapter 5). One of the authors recalls an example of a Master’s student who wanted to study truancy; the student had the permission of the school principal, turned up on the day to commence the research with the school truants, only to find that they had truanted, and were not present! The same is true for sensitive research. For example, let us suppose that one wished to research child abuse in primary school students; the last people to consent, or even to be identified and found, might be the child abusers or those children who have been abused; even if they were identified and found, why should they agree to being interviewed by a stranger who is conducting research? Or, let us suppose that one wished to investigate the effects on teachers in hospitals of working with HIV-positive children in hospital; those teachers might be so traumatized or emotionally exhausted at the end of a day’s work that the last thing they want to do is to talk about it further with an outside researcher whom they have never met before; they simply want to go home and ‘switch off’. These are real issues, and we authors have experienced them with our research students. The researcher has to check out the situation before embarking on a fully worked-out plan, because the plan might come to nothing if useful access is not possible.
It is not only the people with whom the researcher is working that have to be considered; it is the researcher herself/himself. For example, does the researcher have the right personality, dispositions, sympathies, interpersonal skills, empathy, emotional intelligence, perseverance and so on to conduct the research? For instance, it would be a likely disaster if a researcher were to be conducting a piece of research on student depression if the researcher tacitly believed that students were just lazy or work-shy and that they used ‘feeling down’ (as she put it) as an excuse, i.e. who refused to recognize the seriousness of depression as a clinical condition or as a pathological disorder. Equally, it would be an unwise researcher who would choose to conduct a study if she had limited perseverance or if she knew that she was going to move overseas in the near future.
Further, researchers themselves will need to decide whether they have sufficient expertise in the field in which they want to do the research. It could be dangerous to the researcher and to the participants if the researcher were to be comparatively ignorant of the field of the proposed research, as this could mean that direction, relevance, prioritization or even safety might be jeopardized. This is a prime reason for the need for the researcher to conduct a literature review, to demonstrate that she/he is sufficiently versed in the field to know what to do, what to look for, and where, when and how to proceed.
Researchers will also have a personal commitment to the research; it may help to further their specialist interest or expertise; it may help to establish their reputation; it may make for career advancement or professional development. These considerations, though secondary perhaps in choosing a piece of research, nevertheless are important features, given the commitment of time and effort that the research will require.
In addition to access, there are issues of time to be considered. Part of the initial discipline of doing research is to choose a project that is manageable – can actually be done – within the time frames that the researcher has at her/his disposal. So, for example, it would be ridiculous for a researcher to propose to conduct a longitudinal study if that researcher only has maybe six or nine months to plan, conduct and report the entire research project. The time frames may prevent certain types of research from being conducted.
Similarly, the time availability of the researcher has to be considered: many researchers are part-time students who may not have much time to conduct research, and often their research is a lonely, one-person affair rather than a group affair that has a team of full-time researchers. This places a practical boundary around what can and cannot be done in the research. Again, these are real issues. Not only does the issue of availability of the researcher feature in ensuring that the research can be conducted, but this also applies to the participants: are they willing and able to give up their time in participating in the research, for example, not only in being interviewed, but in keeping diaries, conducting follow-up debriefings, participating in focus groups and writing reports of their activities?
Whilst access and time are important factors, so is the issue of resources (e.g. human, material). For example, if one is conducting a postal survey there are costs for printing, distribution, mail-back returns and follow-up reminders. If one is conducting a questionnaire survey on a large, dispersed university campus then one will need the cooperation of academic and administrative staff to arrange for the distribution, collection and return of the questionnaires. If one is conducting an online survey of teachers’ views of such-and-such, e.g. government assessment policy, can it be assured that all teachers will have access to the online facilities, at times that are convenient for them, and that poor connectivity, slow speed and instability of the system will not end in them abandoning the survey before it is completed?
If one is conducting an analysis of trends in public education in early twentieth-century Scotland, then one needs to have time to search and retrieve public records (and this may involve payment), maybe to visit geographically dispersed archives, and time to sit down in front of microfiche readers or computers in public record offices and libraries.
A further consideration in weighing up the practicalities of the research is whether, in fact, the research will make any difference. This is particularly true in participatory research. As Hopkins (1985: 47) remarks, researchers may wish to think twice before tackling issues about which they can do nothing or over which they may exert little or no influence, such as changing an education or schooling system, changing the timetabling or the catchment of a school, changing the uses made of textbooks by senior staff, changing a national or school-level assessment system. This is not to say that such research cannot or should not be done; rather it is to ask whether the researcher’s own investigation will do this, and, if not, then what the purposes of the research really are or can be.
Many researchers who are contemplating empirical enquiries will be studying for a degree. It is important that they will be able to receive expert, informed supervision for their research topic. Indeed, in many universities a research proposal will be turned down if the university feels that it is unable to supervise the research sufficiently. This will require the student researcher to check out whether his/her topic can be supervised properly by a member of the staff with suitable expertise, and many students find this out before even registering with a particular university. It is a sound principle.
A final feature of practicality is the scope of the research. This returns us to the opening remarks in this chapter, concerning the need to narrow down the field of the study. Principally, we advise a single piece of research to be narrow and limited in scope in order to achieve manageability as well as rigour. As the saying goes ‘the best way to eat an elephant is one bite at a time’! Researchers will need to put clear, perceptible, realistic, fair and manageable boundaries round their research. If this cannot be done straightforwardly then maybe the researcher should reconsider whether to proceed with the planned enterprise, as uncontrolled research may wander everywhere and actually arrive nowhere. Part of the discipline of research is to set its boundaries clearly and unequivocally. In choosing a piece of research, the manageability of setting the boundaries is an important issue; if these cannot be set, then the question is raised of the utility of the proposed endeavour.
For example, if one were to investigate students’ motivations for learning, say, biology, this would involve not only identifying a vast range of independent variables, but also handling likely data overload, and ensuring that all the theories of motivation were included in the research. This quickly goes out of control and becomes an impossible task. Rather, one or two theories of motivation might be addressed, within a restricted, given range of specified independent variables (unless, of course, the research was genuinely exploratory), and with students of a particular age range or kind of experience of biology.
Small samples, narrowly focused research, can yield remarkable results. For example Axline’s Dibs in Search of Self (1964) study of the restorative and therapeutic effects of play therapy focused on one child, and Piaget’s (1932) seminal theory of moral development, in his The Moral Judgement of the Child, focused on a handful of children. In both these cases the detailed carefully bounded research yielded great benefits for educationists.
Practical issues, such as those mentioned here, often attenuate what can be done in research. They are real issues. The researcher is advised to consider carefully the practicability of the research before embarking on a lost cause in trying to conduct a study that is doomed from the very start because insufficient attention has been paid to practical constraints.
In deciding whether to embark on a particular piece of research, it is often useful for the researcher to consider the role of the research questions and the guidance to the investigation that they might provide. Some research – often qualitative (Bryman, 2007b) – may not have research questions. Similarly it is important to recognize that research methods are not always driven by the research questions (Bryman, 2007b: 18), and that one should avoid the ‘dictatorship of the research questions’ (Bryman, 2007b: 14) in steering the design and conduct of the enquiry. Nevertheless, in many kinds of research the research questions figure significantly, and hence the chapter moves to considering their importance.
Some kinds of research (e.g. ethnography) might not begin with research questions but, in their closing stages, might use open-ended research (e.g. an ethnography, survey or focus groups) to raise research questions for further study in subsequent investigations. Such research, being exploratory in nature, might not wish to steer the enquiry too tightly, and, indeed, one of the features of naturalistic research (see Chapter 11) is that it endeavours not to disturb the everyday, natural setting for the participants. However, for many kinds of research, one of the early considerations that researchers might wish to address in choosing a project is the research questions that the study might generate (or should, as they derive from the overall purposes of the research).
In considering the proposed research, a useful approach is to brainstorm the possible areas of the field, moving from a general set of purposes to a range of specific, concrete issues and areas to be addressed in the research, and, for each, to frame these in terms of one or more research questions (or in terms of a thesis to be defended).
It is the answers to the research questions that might provide some of the ‘deliverables’ referred to earlier in this chapter. A useful way of deciding whether to pursue a particular study is the clarity and ease in which research questions can be conceived and answered. As mentioned in more detail in the next chapter, research questions turn a general purpose or aim into specific questions to which specific, data-driven, concrete answers can be given. Questions such as ‘what is happening?’, ‘what has happened?’, ‘what might/will/should happen?’ (cf. Newby, 2010: 67–9) open up the field of research questions. Chapter 4 also mentioned causal questions. Here ‘what are the effects of such-and-such a cause?’ and ‘what are the causes of such-and-such an effect?’ are two such questions, to which can be added the frequently used questions ‘How?’ and ‘Why?’. These questions ask for explanations as well as reasons.
Research questions can concern, for example:
Prediction;
Understanding;
Exploring;
Causation;
Testing;
‘What?’;
‘What if:’;
‘Who?’;
‘When?’;
‘Where?’;
‘Why?’;
‘How?’;
Explanation;
Description;
Relations (e.g. between variables, people, events);
Comparisons;
Correlations;
Processes;
Factors;
Evaluation;
Function or purpose;
How to achieve certain outcomes;
Types of something;
Properties and characteristics;
Stages of something;
How to do something;
How to achieve something;
Structures of something (cf. University of Berkeley, 2002);
Alternatives to something;
How to improve or develop something.
Chapter 1 drew attention to numerical, non-numerical and mixed methods research questions. Some research questions might only need to be answered by gathering numerical data; others by only qualitative data. However, we recommended in that chapter that, for mixed methods research, attention should be paid to the research questions such that they can only be answered by mixed – combined – types of data, or by adopting mixed methodologies, or by having a set of purposes that can only be addressed by mixed methods, or by taking mixed samples, or by having more than one researcher on the project (mixed researchers), in short, by building a mixed methods format into the very heart of the research (which goes beyond simple triangulation, as discussed in Chapter 10). So, a research question in this vein might combine ‘how’ and ‘what’ into the same research question, or ‘why and who’ might be combined in the same question, or description and explanation might be combined, or prediction, explanation and causation might be combined, and so on. We provided examples of these in Chapter 1.
It has been suggested (Bryman, 2007b) that in mixed methods research the research question takes on added prominence in guiding the research design and sampling, yet it is often more difficult to frame research questions in mixed methods enquiries than in single paradigm research (e.g. quantitative or qualitative) (Onwuegbuzie and Leech, 2006a: 477). This is because it requires quantitative and qualitative strategies to be addressed within the same research questions. Onwuegbuzie and Leech (2006a: 483–4) provide examples of mixed methods research questions, such as ‘What is the relationship between graduate students’ levels of reading comprehension and their perceptions of barriers that prevent them from reading empirical research articles?’ Here both numerical and qualitative data are required in order to provide a complete answer to the research question (e.g. numerical data on levels of reading comprehension and qualitative data on barriers to reading articles (p. 484)). They provide another example (p. 494) of mixed methods research questions thus: ‘What is the difference in perceived classroom atmosphere between male and female graduate students enrolled in a statistics course?’ This could involve combining measures with interviews.
Here is not the place to discuss the framing of research questions. Rather, we wish to draw attention to research questions per se – in particular their clarity, ease of answering, comprehensiveness, comprehensibility, specificity, concreteness, complexity, difficulty, contents, focus, purposes, kinds of data required to answer them and utility of the answers provided – to enable researchers to decide whether the particular piece of research is worth pursuing. This will require researchers to pause, generate and reflect on the kinds of research question(s) required, before they decide whether to pursue a particular investigation. This is not to say that a study must require ‘plain sailing’ in its research questions; it is to argue that researchers may wish to consider whether they really want to embark on an enquiry whose research questions are too difficult or complex to answer within the scope or time frames of the study. Many of the most useful pieces of research stem from complex issues, complex research questions and ‘difficult-to-answer’ research questions.
Further, researchers may wish to ponder on whether they want to embark on investigations that have no clearly defined research questions or, indeed, any research questions, for example an ethnography, a naturalistic observational study or qualitative research (Bryman, 2007b).
A literature review is an essential part of many kinds of research, particularly so if the research is part of a thesis or dissertation. It serves many purposes, for example:
it ensures that the researcher’s proposed research will not simply recycle existing material (reinventing the wheel), unless, of course, it is a replication study;
it gives credibility and legitimacy to the research, showing readers that the researcher has ‘done his/her homework’ and knows the up-to-date, key issues, and the theoretical, conceptual, methodological and substantive problems in the field in which the research is being proposed;
it clarifies the key concepts, issues, terms and the meanings of these for the research;
it acts as a springboard into the researcher’s own study, raising issues, showing where there are gaps in the research field, and providing a partial justifi-cation for the research or a need for it to be undertaken;
it indicates the researcher’s own critical judgement on prior research or theoretical matters in the field and, indeed, provides new theoretical, conceptual, methodological and substantive insights and issues for research;
it sets the context for the research and establishes the key issues to be addressed;
it makes clear where new ground has to be broken in the field and it shows where, how and why the proposed research will break that new ground and/or plug any gaps in the current field.
A literature review must be useful, not only to show that the researcher has read some relevant materials, which is a trivial, self-indulgent reason, but that this actually informs the research. A literature review must be formative and lead into, or give rise to, all aspects of the research: the field, the particular topic, the methodology, the data analysis and implications for future research. Amongst other kinds of written or online materials, a sound literature review will include up-to-date information from materials such as: books, articles, reports, research papers, newspaper articles, conference papers, theses, reviews, government documents, material from databases and internet sources, primary and secondary sources and so on.
The researcher who is contemplating conducting a particular piece of research will need to give careful consideration to the necessary size and scope of the literature review, as this has implications for time, manageability, practicability and decision making on whether the project is too large, unfocused, diffuse, general or difficult to have justice done to it in the time and resources available. It is a determinant of whether to opt for a particular piece of research.
This chapter has set out several practical considerations in choosing a research topic. We advise researchers, both novice and experienced, to approach the selection of, and decision making on, a research topic with caution, going into it ‘with their eyes open’, aware of its possible pitfalls as well as its benefits and implications. We summarize the points discussed in the chapter in Box 6.1.
BOX 6.1 ISSUES TO BE FACED IN CHOOSING A PIECE OF RESEARCH
1 Make the topic small. Think small rather than big.
2 Limit the scope and scale of the research.
3 Think narrow rather than broad.
4 Keep the focus clear, limited, bounded and narrow.
6 Be realistic on what can be done in the time available, and whether, or how much, this might compromise the viability or worth of the research.
7 Make it clear what has given rise to the research – why choose this topic/project.
8 Choose a topic that might enable you to find your niche or specialism in the research or academic world or which might help to establish your reputation.
9 Decide why the research is important, topical, interesting, timely, significant, original, relevant and positively challenging.
10 Decide what contribution the research will make to the conceptual, practical, substantive, theoretical, methodological fields.
11 Choose a research project that will be useful, and decide how and for whom it will be useful.
12 Decide why your research will be useful and who will/might be interested in it.
13 Decide what might be the impact of your research, and on whom.
14 Choose a topic that is manageable and practicable.
15 Choose a topic that will enable rigour to be exercised.
16 Choose a topic that has clear boundaries or where clear, realistic, fair boundaries can be set.
17 Decide what the research will ‘deliver’.
18 What will the research do?
19 What will the research seek to find out?
20 Choose a topic for which there is a literature.
21 Decide whether you will have the required access and access to what/whom in order to be able to conduct the research.
22 Decide what can and cannot be done within the time and timescales available.
23 Decide what can and cannot be done within the personal, people-related, material, effort-related, financial and scope of the research.
24 Consider the likely clarity, scope, practicability, comprehensiveness, ease of answering, framing, focus, kinds of data required, comprehensibility of the research questions and their combination.
25 Consider whether the research will influence, or make a difference to, practice, and, if not, why it might still be important.
26 Consider whether you have the right personality, characteristics, experience and interpersonal behaviour to conduct the proposed piece of research.
27 Consider whether the research will sustain your creativity, imagination, positive attitude and motivation over time.
28 Choose a topic for which you know you will be able to receive expert, informed supervision.
29 Be clear on why you – personally, professionally, career-relatedly – want to do the research, and what you personally want out of it, and whether the research will enable you to achieve this. How will the research benefit you?
30 How will the research benefit the participants?
31 How will the research benefit the world of education?
32 Choose a topic that will sustain your interest over the duration of the research.
33 Consider whether you have sufficient experience, skills and expertise in the field in which you want to conduct the research for you to be able to act in an informed way.
34 Consider whether it is advisable to embark on a piece of research that deliberately does not have research questions.
35 Consider the necessary complexity (where it exists) of the research phenomenon, scope and conduct of the research, and the difficulty of the research issues, foci and conduct.
36 Consider how future research will be able to build on your research, i.e. that the research opens up possibilities rather than closes them down.
Companion WebsiteThe companion website to the book includes PowerPoint slides for this chapter, which list the structure of the chapter and then provide a summary of the key points in each of its sections. This resource can be found online at www.routledge.com/textbooks/cohen7e.