Process of Constructing the Research Problem

1. Point of Departure

Researchers can use different points of departure to elaborate their research problem. Concepts, theories, theoretical models relating to the phenomenon they wish to study, methodological approaches or tools, facts observed within organizations, a field-study opportunity, a general theme of interest, or a com­bination of these may be used. Studying a well-known research problem using a new methodological approach, using an existing theory to study a new phe­nomenon or re-examining theories (in light of the problems encountered by managers, for example) are all possible routes to take in elaborating a research problem.

1.1. Concepts, theories and theoretical models

Reading over published research works with a critical eye can reveal conceptual contradictions, gaps or inadequacies within the body of theoretical knowledge on a given subject. Strange constructs, theoretical inadequacies in some models, contradictory positions among researchers, heterogeneous research designs, concepts or study contexts, are all openings and, therefore, opportunities for constructing a research problem.

A large number of researchers have used the insufficiencies of existing theo­ries (see the following example) or a comparison of two contradictory theore­tical frameworks as starting points in constructing their research problems. In this connection, articles synthesizing the current state of a theme or a particular concept are often useful bases on which to construct a research problem.

Example: Starting from existing theories

Steers (1975) reviews 17 multivariate models of organizational effectiveness. Organizational effectiveness is defined as the efficiency with which an organization acquires and uses its resources within a given environment. The author compares these models along four dimensions: primary evaluation criteria, nature – descrip­tive versus normative – generalizability and derivation – and synthesizes their inadequacies. His analysis starts from the observation that the concept of organiza­tional effectiveness is rarely defined in existent literature, even when it is expressly referred to. While the author does not himself explicitly choose a new perspective from which to study organizational effectiveness, his remarks and observations on the dimensions of the concept are still angles from which to elaborate new research problems.

For example, following on from Steer’s work, one could think of introducing a social dimension in the concept of organizational effectiveness, a dimension that is often overshadowed in theoretical works. The research could thus aim to answer the following question: ‘What is the social dimension of organizational effectiveness?’

Detecting inadequacies or contradictions in theories or in definitions of existing concepts is one useful method for starting research. Using a theory or theoretical perspective to study phenomena other than those to which it has until now been applied can also form an interesting basis on which to elaborate research problems (see the following example). Finally, we can simply choose to test certain theoretical principles that have already been advanced, but have not yet been convincingly tested.

Example: Using an existing theoretical perspective to study a new phenomenon

Tracy (1993) proposed to use the living systems theory developed by Miller (1978) for studying organizational behavior and management. He focused his analy­sis on usual organizational topics and phenomena – in particular, organizational structure – to which the living systems theory has already been applied, and pro­posed a synthesis of this research. In this article, Tracy outlines the general precepts of the theory and then details its underlying assumptions and theoretical implica­tions. The article offers a good introduction for those interested in constructing a research problem using this theoretical framework.

From Tracy’s work, one could envisage studying organizational configurations using the living systems theory. This theory proposes in fact a typology of the sub­systems involved in the organization of living systems, identifies the properties and the role of actors and suggests how to regulate the system transversally. The initial research question could be: ‘How can the specialization of skills be managed within organizations?’ The research goal would be to construct a typology of company configurations according to the organizational goals and environment – that is, using the living systems theory.

1.2. Starting from a methodology

While, at the moment, most research problems in management science seem to find their genesis in theoretical and conceptual thinking, the methodo­logical approaches or tools used can also constitute interesting starting points for elaborating a research problem. Two possibilities are here available to the researcher. First, the research problem may consist of examining existing methods or methodological approaches, identifying their limits and attempting to propose new ones (see following example). One could propose a new scale for measuring performance, or a new method to analyze discourse, or to support decision-making, for example.

Example: Using a methodology

Eden et al. (1983) set out to design a method to support strategic decision-making in groups. Two assumptions underlie this research project: first, that creating consensus in a group while taking into account the particularities of its members’ individual visions is difficult and, second, that traditional group decision-making methods rely on formal approaches. The research goal, therefore, was to design a decision-making method that accounted for potential differences in managers’ representations of their problems, and that would facilitate consensus and creative resolution of strategic problems. The method they proposed used cognitive map­ping techniques (see Chapter 16). Through cognitive mapping, managers’ repre­sentations are elicited and then aggregated. These aggregates are then discussed in groups, which enables the strategic problems encountered to be resolved creatively.

The other possible route is to use a new method or a new methodological approach to tackle a theoretical research problem that has already been the subject of other research. In this case, however, researchers should be careful to justify from the start the research problem they are studying (drawing on one of the configurations described in the previous section). Moreover, any method used implies a certain number of constraints that will, to a certain extent, limit the investigation. Many methods, for instance, fall within a given epistemological tradition or involve particular theoretical assumptions that are not necessarily made explicit. It is then very useful to pay attention to such considerations before deciding upon a particular research method. Researchers should weigh up all restraints inherent in the method used, and should evaluate their impli­cations at a theoretical level.

Example: Tackling a classic research problem through a new method

Barr et al. (1992) began their research with the following question: ‘Why is it that, in the same environment, and whatever the quality and expertise of their man­agement teams, certain companies are able to adapt and renew themselves while others cannot – and decline inexorably?’ Considering the limitations of classic theoretical frameworks, the authors chose to study the problem of organizational renewal from a cognitive perspective. They developed and analyzed organiza­tional cognitive maps of two companies and then linked their conclusions to organizational learning theory.

1.3. Starting from a concrete problem

Companies’ difficulties and managers’ questions are favorite starting points for research in management. A research problem constructed on this basis ensures interest in the project from a managerial point of view. However, we need to make sure that, eventually, we also find a theoretical perspective on which the research problem and design will both rely.

1.4. Starting from a research setting

Some researchers begin their investigations with a research setting already in mind. This is very often the case when companies enter into research agree­ments: the researcher and the company agree on a relatively general research topic, for which precise modalities then have to be defined. In such a situation, the construction of a research problem will often be influenced by managerial considerations.

In the case of particularly inductive research, for example, when an inter­pretative approach is used (see Gioia and Chittipeddi, 1991), researchers often start with a very broad question in mind and a research setting in which to carry out their enquiry. Their research problem will only truly emerge as they gain a clearer understanding of the context (see Section 1). There are, however, disadvantages in setting off on a field study without a specific research problem (see Section 2.2).

1.5. Starting from an area of interest

Finally, many researchers will naturally be drawn towards studying a particular theme. However, interest in a particular domain does not constitute a ‘question’ as such. The theme the researcher is interested in must then be refined, clarified and tested according to theories, methodologies, managerial interests or pos­sible fieldwork opportunities, so as to elaborate a research problem as such. Researchers might look for any theoretical gaps in the chosen domain, review the concepts most frequently invoked and the methods most often used, or question whether other concepts or methods may be relevant; or identify managers’ pre­occupations. Researchers have to consider what they can bring to the subject, and what field opportunities are available to them.

2. ‘Good’ Research Problems

Beyond the various starting points mentioned previously, there are no recipes for defining a good research problem, nor any ‘ideal’ routes to take. On top of this, as we have seen, researchers subscribing to different epistemological paradigms will not define a ‘good research problem’ in the same way. We can, nevertheless, try to provide researchers with some useful guidelines, and warn them against possible pitfalls to be aware of when defining their research problem.

2.1. Delimiting the research problem

Be precise and be clear Researchers should always endeavor to give them­selves as precise and concise a research problem as possible. In other words, the way the research problem is formulated should not lend itself to multiple interpretations (Quivy and Van Campenhoudt, 1988). For example, the ques­tion ‘What impact do organizational changes have on the everyday life of employees?’ is too vague. What are we to understand by ‘organizational changes’? Does this mean structural change? Changes in the company’s strategy? Changes in the decision-making process? We would advise this researcher to put his or her research problem to a small group of people, and to invite them individually to indicate what they understand it to mean. The research problem will be all the more precise when interpretations of it converge and correspond to the author’s intention.

Having a precise research problem does not mean, however, that the field of analysis involved is restricted. The problem may necessitate a vast amount of empirical or theoretical investigation. Having a precise research problem simply means that its formulation is univocal. In this perspective, researchers are advised to avoid problems that are too long or confused, which prevent a clear understanding of the researcher’s objective and intention. In short, the research problem must be formulated sufficiently clearly to ground and direct the researcher’s project.

Be feasible In the second place, novice researchers or researchers with limited time and resources should endeavor to give themselves a relatively narrow research problem:

As I tell my students, your aim should be to say ‘a lot about a little problem’. This means avoiding the temptation to say ‘a little about a lot’. Precisely because the topic is so wide-ranging, one can flit from one aspect to another without being forced to refine and test each piece of analysis.

(Silverman, 1993: 3)

If a research problem is too broad, researchers risk finding themselves with a mass of theoretical information or empirical data (if they have already started their fieldwork) which quickly becomes unmanageable and which will make defining the research problem even more difficult (‘What am I going to do with all that?’). In other words, the research problem must be realistic and feasible, i.e. in keeping with the researcher’s resources in terms of personality, time and finances. This dimension is less problematic when researchers have significant time and human resources at their disposal (see Gioia and Chittipeddi, 1991).

In short, a relatively limited and clear research problem prevents the researcher from falling into the trap of what Silverman (1993) calls ‘tourism’. Here, Silverman is referring to research that begins in the observational field, without any precisely defined goals, theories or hypotheses, and focuses on social events and activities that appear to be new and different. There is a danger here of overvaluing cultural or subcultural differences and forgetting the common points and similarities between the culture being studied and that to which one belongs. For instance, a researcher who is interested in managers’ work and restricts his or her attention to their more spectacular interventions would be forgetting aspects that are no less interesting and instructive – for example, the daily and routine aspects of the manager’s work.

Be practical As their theoretical or empirical investigative work proceeds, researchers can clarify and narrow down their research problem. If they are initially interested in a particular domain (organizational learning for instance), they may formulate a fairly broad initial question (‘What variables favor organizational learning?’). They may then limit this question to a particular domain (‘What variables favor organizational learning during the strategic planning process?’) and/or specify the conceptual framework they are inter­ested in (‘What cognitive or structural variables favor organizational learning during the strategic planning process?’). Through this narrowing down, the theoretical and empirical investigation will be guided and then easier to conduct.

Conversely, one should avoid confining oneself to a very narrow research problem. If the problem involves conditions that are too difficult to meet, the possibilities for empirical investigation may be greatly reduced. Similarly, if researchers focus too soon on a specific question, they may shut themselves off from many research opportunities that might well have broadened the scope of their research problem. They also risk limiting their understanding of the context in which the phenomenon studied is taking place. Finally, if researchers limit their research problem too much when it has been little studied, they may have only few theoretical and methodological elements to draw on when begin­ning their fieldwork. They will then have to carry out an exploratory theoreti­cal work to redefine their initial research problem.

In sum, it appears difficult to strike a balance between a too large research problem that is impossible to contain, and a too limited research problem that shuts off study opportunities. This is one of the major difficulties researchers will confront when starting out on a research project.

2.2. Recognizing the assumptions underlying a research problem

Scientific Goal Beyond the qualities of clarity and feasibility, the research problem must possess qualities of ‘relevance’. Quivy and Van Campenhoudt (1988) define ‘relevance’ as the general mode and intention – explicative, nor­mative, moral or philosophical – underlying a research problem. A research problem is ‘relevant’ if its underlying intention is understanding or explaining reality (which are the overriding goals of science). ‘Do bosses exploit workers?’ ‘Is work flexibility socially fair?’ ‘What are the organization’s aims?’ are questions that translate moral (in the case of the first two) and philosophical intentions (in the case of the last one). But in our opinion, the principal aim of the social sciences is not to make moral judgements about the functioning of organizations – even if a moral or political concern may inspire a research problem (Parker, 1993; 1994). The social sciences lack sufficient methods to answer philosophical problems – even if philosophical thinking, through epistemology in particular, is essential to the development of these disciplines. In sum, a research problem must translate into a knowledge project, whether comprehensive, explicative or predictive.

Underlying values and assumptions While a research problem should not have a ‘moral’ or ‘political’ intention, researchers must be aware of and question its underlying values and assumptions (others than the epistemological assumptions we have mentioned earlier in this chapter). For example, and it is particularly true in management sciences, some research problems are stamped with the idea that research enables humanity to progress and the organiza­tion’s efficiency to be improved. For instance, the research problem ‘how can we improve organizational learning?’ conceals the assumption that organizational learning improves the organization’s efficiency or the employees’ well-being. But is it necessarily so?

Because of the strong influence of trends in managerial and economic think­ing, one must be particularly wary of concepts and notions that contain the idea of progress or improvement in efficiency in management science – in relation, for instance, to culture, change, consensus or communication. But, as Silverman (1993: 5) puts it, ‘an uncritical belief in “progress” is an unacceptable basis for scientific research’. In our opinion, researchers should question the assump­tions and values underlying their research problem and that will influence their research design and methodology and, therefore, their research results and impli­cations. To return to our initial example, why should we assume that organi­zations must learn, that they must have a ‘strong’ culture, that the environment changes more quickly today than before, or that shared meanings and consensus in the organization improve its functioning and efficiency? Are these assump­tions based on some reality? Or are they the expression of our current values and ways of thinking: new imperatives that replace those of the scientific work organizations of the 1920s?

Silverman (1993) here calls researchers to use a historical, cultural and politi­cal sensitivity in order to detect the interests and motivations behind their research problem and to understand how and why these ‘problems’ emerge. Why is there more interest in, and therefore more research problems about, organizational learning today? What does this sudden interest in ‘environmental issues’ mean? Such questions can help us to understand how and why these new ‘realities’ emerge. They also encourage us to look critically at the way we formulate our research problems, thus freeing ourselves from some taken-for- granted beliefs about organizations.

3. Constructing a Research Problem: Illustrations

Given the difficulties outlined above, constructing a research problem is rarely a matter of taking just one of the routes we have presented. It is often a case of moving back and forth between theoretical and empirical steps. A general research problem stemming from an initial review of existent literature may prove flawed when the concepts it relies on are operationalized or may be too broad to investigate with limited means and resources. In the following, we present two examples of paths taken by researchers in constructing a research problem. These different experiences are not presented as model examples. To the contrary, they are intended to show the diversity of processes that may be followed and the difficulties that may be encountered when constructing a research problem.

A linear dynamic A research problem can emerge clearly and quite quickly after research has begun. As the example described below shows, combining two theoretical approaches (the evolutionist theory and the theory of non-linear dynamic systems) to analyze a relatively classic phenomenon (the management of innovation) enables one to compose an original research problem relatively early in the research process.

Example: A question resulting from the confrontation between two theoretical fields

My research question was directly inspired by my training. As a graduate in pure mathematics, I sought to use my theoretical knowledge to gain a better understand­ing of organizations. My thesis was based on studying the evolution dynamics of a group of innovation projects. I started from chaos theory, with which I was familiar, and I chose to apply it to the management of innovation principally because it appealed to me. While reviewing related work on the subject, I noticed that innova­tions were rarely studied at the level of a population, and that their evolution dynam­ics was non-linear. I then thought of using evolutionary theory to build a model of the laws underlying the evolution of this population. I discovered that parametric mod­els were potentially chaotic. This drew my ideas together and I had my research prob­lem: ‘How does a population of innovation projects live and die?’ Once I had posed my research problem, my research work consisted of testing this conceptual framework.

A recursive dynamics While the process followed in the previous example seemed to unfold without great difficulty, the construction of a research problem is often less linear. A lot of research begins on ill-defined theoretical and methodo­logical bases. The difficulties will be all the greater if the researcher chooses to work from an original or little-known epistemological perspective. The following example illustrates a more treacherous route. This young researcher was initially interested in the process of knowledge capitalization within an organization. After theoretical reflection on the subject, she redefined her research problem and focused on the collective construction of knowledge. Her research problem then seemed to be clear enough: ‘How does collective knowledge construct itself within organizations?’ This redefinition led her to conduct new theoretical investigations, but she has had trouble developing an empirical vision of her research problem. Her choice of constructivism as her epistemological position has numerous implications in the construction of her research problem. After an initial explo­ratory empirical phase, she now feels that synthesizing her initial observations will enable her to specify the practical terms of her research problem.

Example: A research problem resulting from theoretical reflection in the constructivist perspective

I began my thesis in December and I’ve already taken three months to arrive at a satisfactory research problem. When I first started on my thesis, I wanted to study the process of knowledge capitalization within organizations. This is an important managerial problem that interests many companies. However, I quickly reached my first impasse: firstly, a thesis had already been written on a closely related subject, and secondly, it seemed important to me to tackle the problem of knowledge construction before that of its capitalization.

Over the following three months, I read through published works with a new research problem in mind. I wanted to know how knowledge was collectively constructed and to understand its dynamics within organizations. This is a subject that had never really been dealt with at the level at which I wished to study it, that of working groups. I skimmed through some writings on knowledge in different domains and eventually took the direction of an American model of social psy­chology. However, I found it difficult to integrate this very heterogeneous reading material in the way I had hoped.

Over the summer I found a company that was interested in my research, and I had to begin to actively put together an initial conceptual framework (very perfunctory to start with) and to delve into epistemological and methodological considerations. However, I didn’t know how to observe knowledge construction and was not really sure which information to collect. I opted for a very inductive process.

After around three months of fieldwork, I have neither completely resolved these methodological questions nor really defined my epistemological position. I am now synthesizing my first field results, which I hope will enable me to clarify these points and specify my research problem.

Finally These two ‘stories’ are, of course, far from being comparable. They reflect different states of advancement in the research process (the research has been completed in the first example, but is ongoing in the second). However, they illustrate some of the difficulties researchers can come up against when they are trying to construct their research problem. In addition to the difficulties engen­dered by theoretical investigation and by drafting an initial broad research prob­lem, researchers often meet instrumentation problems or empirical constraints that can lead them to redefine their research problem (see Chapter 7). These diffi­culties are even greater when a field opportunity presents itself or when the researcher seeks to define his or her epistemological position. Then it is a question of ‘making the best with what you have’. A researcher might, for example, con­duct an initial exploratory study (as in the two examples cited above) and speci­fy the research problem once he or she has developed an initial ‘understanding’ of the phenomenon studied. Alternatively, the researcher may prefer to wait until he or she has resolved his or her methodological or epistemological problems. We strongly advise researchers who encounter such difficulties to discuss them with their colleagues. The questions they will ask and the efforts at clarification the researcher will be pushed to make will serve as leads, openings and sources of inspiration and structuring that will help to construct a research problem.

Source: Thietart Raymond-Alain et al. (2001), Doing Management Research: A Comprehensive Guide, SAGE Publications Ltd; 1 edition.