Honours thesis in psychology/Guidelines

Honours and master's thesis in psychology guidelines

Acknowledgement: Adapted by James Neill from work by Professor Marie Carroll, University of Canberra.

Overview

This article provides useful advice for the early development of honours and master's psychology thesis projects. It discusses the scope, significance, and types of projects, with warnings about some common pitfalls, to help guide initial thinking and planning.

Scope

Psychological research is conducted for a variety of reasons, such as to:

• establish the existence of a phenomenon
• determine the conditions under which a phenomenon will be observed
• explore correlates of a phenomenon
• test theory-based hypotheses
• test a new method or technique
• indulge a researcher's curiosity
• reduce uncertainty about psychological processes (Sidman, 1960).

No particular type of research is necessarily more legitimate than the others, although some types of research lend themselves to good thesis work.

A good topic for a thesis:

• is of sufficient significance to obtain a high mark if it is executed well
• is manageable within the time and resources available
• allows the candidate to demonstrate his or her research skills.

However, unless the research question is of some psychological significance, wizardry in execution alone will not result in a good mark. Similarly, a brilliant idea which cannot be brought to fruition satisfactorily within the time available will not earn as good a mark as it should. Nor will pedestrian research, such as simply correlating scores on tests, be rated highly.

Significance

Significance means that the thesis must have some implications for psychological theory and/or practice. A difficulty sometimes encountered in this respect is that the candidate is employed by a particular clinical, educational, or industrial organisation and sees an opportunity for helping the agency solve a problem while completing the degree. Ideas of this kind are obviously seductive but can make for very bad theses, because a problem which may be of some significance within a particular organisation can be trivial outside that context. This should not be interpreted as proscribing theses on applied topics which can be marked as highly as theses on so-called "pure" topics. The relevant dimension is not pure versus applied, but significant versus trivial.

The time available in which to complete the project is an important constraint on the choice of topic. Realistic thinking is required so that an otherwise good project is not compromised because there is not sufficient time in which to conduct it. So too, consideration must be given to the resources available. While the discipline may be able to make some contribution if it is considered warranted, the size of any such contribution must of necessity be small.

Try to choose a topic that demonstrates that you have ingenuity as a researcher rather than simply a high threshold for boredom. Ingenuity should not be confused with complexity of instrumentation or data analysis, both of which may be potent sources of error in the wrong hands. Ingenuity in this context is concerned more with the quality of reasoning than with use of different techniques.

Types of projects

Honours and master's thesis topics, as initially posed by candidates, are usually of three main types:

• Pedestrian research
• Formula research
• Theory-driven research.

Pedestrian research

Pedestrian research involves empirical work which is completed without ever setting out to address a theoretically-driven research question. Examples are:

1. Manipulative research of the "lights on/lights off" variety; an independent variable is manipulated (e.g., lights are "on" or "off") and a dependent variable is measured (e.g., mood) but there is no testing of an underlying theory.
2. Applications of a particular data-analytic technique
3. Literal replications of previous studies. Replications can be the beginning of a mature research program but, by themselves, are pedestrian.
4. Crude survey research (e.g., a local polling study to find out "What do students think of the food served in the cafeteria?")

The distinguishing feature of Pedestrian research is that no thought about any issue or problem in psychology is required.

Formula research

In Formula research, a research question is posed, often a significant one, but the method of answering it is straightforward (if time-consuming). Examples are:

1. Norming a psychological test
2. Evaluation of standard procedures in a particular organisation
3. Scaling exercises

The distinguishing feature of Formula research is that the steps followed in providing an acceptable answer to the research question are well known.

Theory-driven research

Theory-driven research involves significant development of both a research question and a strategy for answering the question. Examples are:

1. Comparing two theories with respect to the predictions they make about certain phenomena
2. Testing the implications of a particular theory
3. Constructive, as opposed to literal, replications (cf Smith, 1970)
4. Understanding the processes for change, as distinct from just the outcomes, in evaluation studies.

The defining feature of this type of Theory-driven research is the exercise of imaginative but disciplined thought about a problem of behaviour or experience of some generality.

Which type?

Most supervisors would agree that Pedestrian research is not, and Theory-driven research is, appropriate for fourth-year theses. There may be some disagreement about Formula research as this type forms a major and significant part of applied research in psychology. It can demonstrate some of the skills of research (e.g., analysing and interpreting data, writing effectively) but stresses some (e.g., organising time and resources) to the exclusion of others (e.g., formulating a research question). In short, it demands rather too much perspiration and rather too little imagination. However, if a topic of this type is contemplated, check with your supervisor about its acceptability. It is well to do this early before you invest too much effort and ego in it.

One final point: "Bathtub" theorising divorced from a base of knowledge of the work and thinking of others is not recommended, except as a preliminary exercise. Inspiration is of course the key to first class research, but do not expect inspiration without perspiration. The serendipitous finding is typically preceded by a great deal of hard work.

Sources of ideas

Source of good ideas for theses can be many and varied. A supervisor may suggest some ideas but do not expect a blueprint. Ideas come from your own reading and thought and the more of this the better. After three years of psychology, some questions should have occurred to you as interesting and important and these can serve as a starting point.

One fairly conventional approach to generating research ideas is to immerse yourself in the literature in some particular area of interest, then to engage in some uninhibited divergent thinking (or brainstorming), before picking among the products for the most significant and practicable. Among the suggestions that Marx (1970) makes are the following:

• read with research ideas in mind
• use literature reviews and integrative papers
• don't passively accept the authors' view; play devil's advocate and force the author to persuade you
• look for gaps or discrepancies in observations, data analyses, or in the inferences from them, as this is a common source of research ideas — the conflict of evidence or the missing piece of information
• think of new ways to analyse or interpret data which could bring out points that have been overlooked or may lead to different conclusions to those that have been drawn.

Another important source of research ideas is discussion with your supervisor and other staff members. Your research topic needs to match the interest and expertise of your supervisor to bring out the best in their skills.

Method and design

In a good research study, the research question (horse) comes before the cart (method). It doesn't work so well when the cart (method) comes before the horse (research question).

The nature of the research problem should dictate the method to be used in its investigation — and not the other way around. Although this may seem self-evident, it is not uncommon for the tail to wag the dog. This happens, for example, when a researcher has a fondness for a particular method (or ignorance of other methods) and allows this to set the direction of research. Good theses employ the best method available for investigation of the problem. Where the best method cannot be employed, some rethinking of the problem is called for to make it more tractable, or perhaps a change of topic is required.

A simple classification of research methods in psychology was proposed by Willems (1969) who argued that research methods can be located within a two dimensional space, with one dimension being the extent to which manipulation of antecedent conditions is involved and the other being the extent to which units of measurement are imposed or the observations made. The clinical case study of the sort Freud, for example, reported would fall at the low end of both the dimensions of manipulation and measurement. In the case study, there is no attempt to control the host of variables influencing the individual's behaviour nor is any system of measurement involved in the gathering of data. The laboratory experiment marks the upper end of both dimensions, as the independent variables are strictly controlled and the dependent variable is measured in terms of an interval or ratio scale of measurement.

Methods which are high on both dimensions are not necessarily superior to those which are low on both dimensions. Judgements of this kind cannot be made independently of the problem to which they are applied. However, two rough rules of thumb might be of use to the beginner:

1. methods high on both dimensions are preferred.
2. methods low on either or both dimensions present more "traps for the young player".

Once a method has been selected, get down to the "nuts and bolts" of planning for the project. The major concern here is the overall design of the study, since from this most of the details will flow. There are a variety of conventional designs employed in psychological research, and wittingly or unwittingly, the research plan will probably conform to one of these.

There are two basic problems in research design, which Campbell and Stanley (1963) described as ensuring the internal and external validity of the study. Internal validity is primary as without this external validity is not possible, and much of the methodological criticism of the study will be directed to ensuring that the requirements of internal validity have been met.

Internal validity refers to the correctness of the inferences drawn from the actual observations in the study. The researcher's thinking about the problem leads to expectation of a certain outcome and the study is designed so that the outcome will be realised or, if it is not, that a negative result will have some meaning. The researcher, of course, wishes to conclude that the variables that are the focus of his/her thinking are responsible for the results obtained. But there may be plausible rival interpretations of the results. These arise when variables other than those of interest have not been neutralised as a result of the design employed, and these pose threats to internal validity. It is only when the critic cannot propose a plausible rival interpretation that he or she will be happy to accept the researcher's inference. So the researcher's task is to second guess the critic, to look for weaknesses in the design which will allow alternative interpretations to intrude, and to take steps to remedy these. Correlational designs are particularly troublesome in this regard and should come in for close scrutiny.

External validity refers to the soundness of the generalisations made from the researcher's observations to a wider situation. Some level of generalisation is almost always implied, since statements about a particular set of data obtained under a particular set of conditions are, in and of themselves, not of a great deal of interest. External validity cannot be guaranteed. However, steps can be taken to ensure that some reasonably credible generalisations are possible beyond the particular participants or measures or other aspects of the study that were employed.

A practical suggestion for the design stage is for the researcher to list the variables of concern for the study. This itself may be a salutary exercise as long lists may suggest that the project is unwieldy or messy. Then group the variables into dependent and independent (or quasi-dependent and independent in the case of non-manipulative designs). This will indicate the direction of influence within the variables of interest. In other than purely descriptive projects, which are not as a rule recommended for thesis work, some direction of influence is implied and this should be indicated in labelling the variables. Next, note beside each variable how it is to be measured, selected for, or manipulated and indicate the level of measurement involved. Finally, in a diagram or series of diagrams set out the way in which the variables interact. This may be in terms of, for example, a contingency table, correlation, one-way or factorial design. This final step might be beyond those without a background in research design but it is worth having a shot at. The purpose of planning out the design in this way is to clarify the researcher's thinking (or show how woolly it still is), to pinpoint details that have yet to be worked out, and to suggest a model for statistical analysis that might be required. It will be of considerable value in drafting the proposal.

Proposal

It is a useful discipline to communicate research ideas to others and have them critiqued. Presentation of a proposal to academic staff provides an opportunity to clarify the researcher's thinking about the project and to gain feedback about the adequacy and feasibility of the ideas.

Student researchers are often nervous about the prospect of presenting a proposal to staff. For example, a student researcher may feel inadequately prepared because of the short lead-in time. Staff reviewers appreciate this and do not expect a final and complete version. It is inevitable that there will be gaps in the proposal, but the exercise serves one of its purposes by drawing attention to these. While there is an obvious need for staff to be critical, the purpose of the proposal presentation is not to evaluate the student researcher but to provide feedback towards improving the proposed project, and the atmosphere is accordingly cooperative rather than judgemental.

A range of opinions will be expressed about the proposal; your task is to note and evaluate them. You do not necessarily have to accept them all; it is your project and in the end you must take responsibility for it. Listen to the criticisms, ask for clarification where necessary, and do not be afraid to defend your ideas where you think appropriate.

So that staff do not come to the presentation "cold" it is a good idea to share the proposal with reviewers in advance of the presentation. The proposal should summarise the essential points. Only references central to the thesis should be cited, and full publication details of these sources should be provided. The proposal should include a working title which need not be the title of the finished thesis.

When presenting the proposal, provide a verbal precis of no more than 5 minutes, which will leave 10 minutes or so for comments and questions. The verbal precis should concentrate on stating the problem and the proposed method.

The statement of the problem should answer two questions:

• What is being attempted in the thesis?
• Why? (justification of its importance)

It is surprising how difficult some student researchers find it to articulate in one or two sentences a response to the question: "What are you trying to do?" The question is often met with a "flight into the literature". Important sounding names or concepts are reiterated, but the listener is left none the wiser about the specific purpose of this particular project. It is a useful discipline to attempt to write in one clear sentence the aim of the project. Once this has been done to your satisfaction, the details of the problem can be suitably elaborated.

The answer as to the why the question is being investigated will require an outline of the background to the question and the implications for psychological theory or practice. A detailed review of the literature is not required. Remember the presentation is oral, and listeners, as opposed to readers, are not able to process large chunks of detailed material. Sketch out the argument for why the topic you have chosen needs to be investigated, with essential references. Less pertinent material can be kept in store for answering questions should they arise.

Systematic review of the background to the problem should make its significance obvious, though a brief comment on the implications of an answer to the questions may not be wasted. A statement of the problem should conclude with your specific aim or expectation. The study should be guided by an overarching research question and should have a specific hypothesis (or hypotheses). If specific hypotheses are not available, explain why. It may indicate that you are on a "fishing expedition" (leisurely affairs which often result in catching nothing).

In the Method section, include sub-sections for

1. Design: Describe the study's design and comment on potential confounds and the way in which these threats to validity are controlled for.
2. Participants: Comment on the target population, sample size, sampling frame, recruitment and sampling method, and any specific participant characteristics pertinent to the proposal (e.g., gender, age, dimension on which matching might be contemplated).
3. Materials: Describe the materials and instrumentation to be employed in the project. Comment on the reliability and validity of psychological tests and questionnaires. Lack of information about the chosen measures can be significant weakness in a proposal, with the student researcher being rendered speechless by simple questions such as: "How stable are the scores obtained using this instrument?" or "How do you know the test measures the particular concept in the hypothesis?" Replies such as "I hope so" or "It says so on the label" are insufficient. So, get to know know the proposed instruments and their psychometric properties before the presentation.
4. Procedure: Briefly describe the procedure to be followed in the project's data collection.
5. Ethical issues: What potential ethical issues are of greatest concern? How will these be dealt with?
6. Data analysis: Indicate the nature of the data you expect to obtain and the techniques appropriate for its analysis in order to address the hypotheses. Consider what operations will need to be performed on raw observations to produce testable data (e.g., creating composite scores). Secondly, what analytical tactics will be used? The actual statistical technique to be employed need not be known in detail, but the general approach should be indicated (e.g., correlation between two variables, determination of the difference between means, etc.). Include indicators of effect size.

Briefly sum up the proposal, including what will it mean if the hypothesised results are supported — and what will it mean if they aren't?

By making it clear what you are intending to do and why, reviewers can spend most of the discussion time on the substantive issues raised, rather than trying to work out what is being proposed. Ideally, student researchers want feedback on the merits and demerits of the planned project and this will be facilitated if the presentation is clear and to the point.

In reviewing the proposal, different staff will take different approaches. Some will be concerned with measurement and analysis while others will be more concerned with the fit between what you are actually doing and what you claim to be doing. Still others will focus on the theory from which the study is derived.

When it comes to actually presenting the proposal, the following advice might help:

1. Don't begin by apologising for the proposal. Be confident, whilst acknowledging limitations along the way.
2. Don't talk for too little or too long. Keep to the time limit in mind and pace your presentation so that there is time for discussion.
3. Avoid reading a pre-prepared script word for word. This will tend to bore and frustrate a listener. But it is a good idea to prepare a summary of the essential points on reference cards or a sheet of paper and to speak from these. Bear in mind that the requirements of effective oral and written forms of communication differ.
4. Avoid vague generalisations and unsupported assumptions.
5. Be prepared for criticism. There is no need to be defensive, nor do you need to respond to every counter argument put to you. Be open to contrary opinion when it comes.
6. Before coming to the proposal formulate answers to the following:
   1. What am I attempting to do? Can I verbalise this in a comprehensible way to non-psychologists?
   2. Why am I attempting to do this? Has it been done before? If not, why not? It is because it is a silly idea or because the answer to it is impossible? If it has been done before, why should it be done again?
   3. What is the theoretical orientation of the project? Why have I chosen this particular theoretical orientation? Are there others equally applicable to the problem? If so what are the grounds for my choice?
   4. How do I plan to do it? Are there any gaps between what I want to do and what I will be actually doing? For example, do the instruments I am planning to use really reflect the concepts I am interested in?
   5. What guarantees do I have for access to the population from which participants are to be drawn? What is the plan B?
   6. How will I know when the question is answered? What, specifically, are the results I am expecting?
   7. What are the implications of an answer to the question? For psychological theory? For psychological practice?

Finally, once the dust has settled, reconsider your study in the light of the feedback received. Redesign where necessary and fill in gaps with a further literature search. This is easier to do if you make comprehensive notes of the queries and comments raised during your proposal as soon as possible after the session. Keep these notes to aid you later when you begin drafting the thesis proper. You may be predisposed to overlook some of the awkward points raised, but your critics, if they become examiners, will not.

Conducting the study

Once the design is complete, begin work on the actual conduct of the study. Anticipate delays along the way and some loss of participants, so begin early. It can be good idea to conduct a pilot study to ensure that the procedure works as it should, such as time allows, and to develop a sound routine for administering the procedures. What you are seeking is a standard approach to all participants only varying, in the case of manipulative studies, in those factors of pertinence to the research question. To do this you need to train yourself. For example, prepare a set of instructions and learn them by rote so that you are treating each participant in the same way. The more complicated the procedures the more training you will require.

It is helpful to act as a participant yourself. This allows you to feel what it is like to be on the receiving end, and to anticipate problems that others may have in doing what you ask. Playing the role of the naive participant can alert you to ambiguity and at times, absurdity in the procedure you are employing.

It is important in the conduct of psychological research that you develop a rapport with your participant. This calls for certain social skills which you may have, but which, if you do not, must be learned from observation of others or by self-reflection. An authoritarian approach is not recommended as a way of gaining rapport. Many participants will be apprehensive in the research context, and one way of reducing this is to provide full information on what you are doing and why. At the conclusion of the study, "debrief" participants either verbally or by giving them a written account of the projects aims, and where possible, allow them access to the results.

Treating participants with integrity is not only required to develop rapport but is also a necessary characteristic of an ethical researcher. Where the research raises obvious ethical problems these should be discussed with staff and fellow students and modified until a satisfactory state of agreement is reached. But all psychological research involves some ethical problems (e.g., invasion of privacy and confidentiality) and these should not be lost sight of in the "march of science". Projects require University Human Research Ethics Committee approval before data is collected. Where the project involves some agency outside the university (e.g., hospital patients, school students, members of community groups) you must also obtain the necessary clearance from the agency's own ethics committee (e.g., Health Board, Education Board). This requirement for clearance from an outside ethics committee can mean lengthy delays before you can begin, since meetings may be scheduled only on an infrequent basis. You must anticipate such delays in the planning of your project, and avoid reliance on such organisations unless you are well advanced in your planning.

The essence of empirical research is observation, and in the conduct of the study you should use your powers of observation to the full. Even if the situation is a highly structured one as in a laboratory experiment, it is important not to "switch off" and let the experiment run itself. Be alert for the unexpected result which may signal a problem with the procedures being used, or which may suggest an interesting, but previously overlooked, hypothesis. A potentially important source of information is the report of the participant on completion of the study. The participants' perceptions of the research situation may provide clues to what you are actually doing as distinct from what you think you are doing. The value of this information will depend very much on the nature of the task set.

Data analysis

When all the data are to hand, begin analysis informally, then proceed to the formal treatment you had planned, and finally examine the data in ways which might have suggested themselves during the conduct of the study or the formal data analysis. The preliminary and informal analysis is most important for gaining a "feel" for the data. How systematic are the results you have? What are the trends? Are there data points which are widely discrepant from the majority of observations, the outliers? What might account for these? When small sample sizes are involved, this preliminary analysis can be done by simply scanning the raw data. In the case of larger sample sizes, plotting frequency distributions and scatterplots is probably called for. Exploratory data analysis (see e.g., Velleman & Hoagbin, 1981) will provide the information conventionally summarised in descriptive statistics such as the mean, standard deviation, and correlation coefficient. Compute these at this stage, if they are not to be provided by the formal tests you have in mind, but do not omit the essential first step of "eyeballing" the data.

From this preliminary analysis you should be able to predict what your formal analysis will show (unless you are using a complex multivariate procedure). A discrepancy between prediction and outcome should then alert you to problems with the formal analysis (or with your preliminary analysis) which should be resolved to your satisfaction before proceeding. If you are thoroughly conversant with your data in the manner suggested here, you will be able to draw sound conclusions from them. If you are not, you could find yourself talking nonsense. Bear in mind that "the finding of statistical significance is perhaps the least important aspect of a good experiment" (Lykken, 1968).

References

Bachrach, A. J. (1981). Psychological research: An introduction (4th ed.). Random.

Bordens, K. S., & Abbott, B. B. (1991). Research design and methods: A process approach (2nd ed.). Mayfield.

Campbell, D. & Stanley, J. (1963). Experimental and quasi-experimental designs for research. Rand-McNally.

Lumsden, J. (1973). On criticism. Australian Psychologist, 8, 186-192.

Lykken, D. T. (1968). Statistical significance in psychological research. Psychological Bulletin, 70, 151-159.

Marx, M. H. (1970). Observation,discovery, confirmation, and theory building. In A.R. Gilgen (Ed.), Contemporary scientific psychology. (pp. 13-42).

Mayer, R., & Goodchild, F. (1990). The critical thinker. Brown.

Sidman, M. (1960). Tactics of scientific research. Basic Books.

Smith, N. C. (1970). Replication studies: A neglected aspect of psychological research. American Psychologist, 25, 970-974.

Velleman, P. F., & Hoagbin, D. C. (1981). Application, basics, and computing of exploratory data analysis. Wadsworth.

Willems, E. P. (1969). Planning a rationale for naturalistic research. In E. P. Willems & H. L. Raush (Eds.) Naturalistic viewpoints in psychological research (pp. 44-71). Holt, Rinehart & Winston.