Research goals and research questions
Introduction to Social Research Methodology
From managerial problems to research topics
The managerial problem
Research in organisations rarely begins with a question. It begins with a problem — a gap between how things are and how somebody wants them to be. Our running case this semester makes the point concrete. Meridian is a fictional mid-sized Polish retail-and-services company: around 450 employees, 32 stores, and a growing e-commerce arm. In two years its annual staff turnover has risen from 14% to 27%, and its customer satisfaction scores are falling. The board wants evidence rather than hunches, and the students of this course play the junior research team advising it.
What the board supplies is not a research question but a worry. The distinctive work of this session — and of the early phase of any applied research project — is the journey from that worry to a question that research can actually answer.
Where research topics come from
The key process in identifying a topic is turning an idea or a general concern into a topic that can become a research problem. The advice from the literature is to start not with “what shall I write about?” but with “what do I want to understand or learn about?”. Topics come from several recurring sources:
| Source | Example |
|---|---|
| Practical problems | A turnover spike, a falling satisfaction score, a failing product |
| Existing research | Course readings, subject journals, and studies that leave questions open |
| Prior work | Written work or projects the researcher has already undertaken |
| Received wisdom | “Common sense” claims in the media or the organisation that have never been tested systematically |
In organisational settings the richest source is usually the last one: the gap between what people in the organisation believe and what has actually been checked.
What makes a good research topic?
Before committing to a topic, a researcher should ask five hard questions of it:
- Will anyone care about the answer? — the topic should matter to the organisation or to existing knowledge.
- Is the problem solvable within the time available? — a semester project must fit a semester.
- Will I add something new? — or has the question already been answered well by others?
- Do I have good tools to address this question? — the necessary methods, skills, and data must be within reach.
- What makes me think I will be successful? — an honest audit of one’s own resources.
These questions sharpen the three criteria from session 1 — relevance, feasibility, and ethics — into a practical checklist. Applied to Meridian, “why are people leaving?” passes easily: the board cares about the answer, staff and data are accessible, and a semester is long enough to make genuine progress.
Getting the scope right: too broad
The scope of the research problem underpinning a study must not be too broad; otherwise it becomes very difficult to address the problem adequately in the space and time allowed. A too-broad topic produces three predictable troubles: the researcher finds too many information sources and cannot decide what to include, exclude, or prioritise; the information found is too general to support a clear framework for examining the problem; and the material covers so many concepts and ideas that they cannot be integrated into one coherent study. Labels such as “employee motivation”, “organisational culture”, or “customer behaviour” name entire fields, not topics. Even “staff turnover” is still a field; “why front-line store staff leave Meridian” is beginning to become a topic.
Figure 1 draws scope as a spectrum. At the broad end sits a field, with the three symptoms above; at the narrow end, an incident, with the symptoms described in the next sections; in the middle, the right scope — focused and time-limited, broad enough that the answer matters beyond the case and narrow enough to deliver. The running example sits under each card: “staff turnover” is still a field; “why front-line store staff leave Meridian” has the right scope; “why did the Saturday shift at store 17 resign in March?” is an incident.
Six strategies for narrowing a topic
Six practical strategies help narrow a topic to a manageable scope. The first three slice the subject matter; the last three bound the study’s coverage.
Figure 2 applies each strategy to Meridian in the form not this, but that: the top row slices the subject matter, the bottom row bounds the coverage.
| Strategy | Principle | Meridian illustration |
|---|---|---|
| Aspect | Choose one lens through which to view the problem, or just one facet of it | Not “turnover at Meridian” but “the role of line management in turnover at Meridian” |
| Components | Break the initial variable or unit of analysis into smaller parts that can be analysed more precisely | Not “employees” but “sales staff with under two years’ tenure” |
| Type | Focus on a specific type or class of people, places, or phenomena | Not “all departures” but “voluntary resignations”, setting aside retirements and dismissals |
| Place | The smaller the geographic or organisational unit, the narrower the focus | Not all 32 stores but the five stores with the highest turnover |
| Time | The shorter the time period, the narrower the focus | Not “in recent years” but “since the e-commerce expansion began two years ago” |
| Relationship | Design the study around how two or more specific variables or perspectives relate (cause/effect, compare/contrast, group/individual, problem/solution) | “How does perceived workload relate to intention to quit?” rather than “what is going on with morale?” |
Getting the scope right: too narrow
Narrowing has a limit, and it is important to remain flexible, because a research problem can also be defined too narrowly. A too-narrow problem leads to characteristic troubles: the researcher cannot find enough information, and what is found is tangential or irrelevant; the information is so specific that it cannot lead to significant conclusions; the problem is so case-specific that it limits any opportunity to generalise or apply the results to other contexts; and its significance is limited to a very small, unique population. The goal when defining a research problem is one that is focused and time-limited, but not so narrowly constricted that the opportunity to investigate the topic thoroughly disappears. “Why did the Saturday shift at store 17 resign in March?” is an HR incident, not a research topic — nothing learned from it travels anywhere else.
These are the symptoms on the right-hand card of Figure 1.
Research practicalities
A topic must also survive contact with practical reality. Before committing, the researcher should check:
- Can I physically access the object of my research?
- Are there gatekeepers who can grant or deny access — and will they grant it?
- Will there be political or administrative obstacles?
- Can I actually reach the people I need to interview, survey, or observe?
- Do I have the language skills the study requires?
- If the study uses documents or data that already exist, can I access the materials — in archives, physically, or online?
Ultimately, a good research topic is one that can be investigated with the resources actually available. Studying Meridian’s own staff requires the board’s blessing, which the research team has; studying its competitors’ staff would founder on access, however interesting the comparison might be.
Research goals
Three goals
Babbie identifies three purposes — three goals — that social research serves: exploration, description, and explanation. The goal of a study is not decorative: it determines the kind of question the study asks, and therefore the kind of design it needs. Of any study, and any question, one should ask: which of these is it trying to do?
| Goal | Core question | Character |
|---|---|---|
| Exploration | What could be going on here? | Developing initial familiarity with a phenomenon that is new, surprising, or poorly understood |
| Description | What is happening, to whom, how much, how often? | Measuring and reporting the characteristics of a situation or population |
| Explanation | Why is it happening? | Identifying causes, reasons, and mechanisms; relating variables to one another |
Figure 3 compares the three goals column by column: the question each asks, when it is appropriate, what it typically involves, what it produces, and its Meridian version at the bottom. The sections below take the goals one at a time.
Exploratory research
Exploratory research is appropriate when a phenomenon is new, poorly understood, or surprising — when the researcher does not yet know enough even to ask precise questions. Its ambitions are deliberately modest: to satisfy initial curiosity and build familiarity with the terrain; to discover what the relevant factors, categories, and concepts even are; to test the feasibility of a larger and more structured study; and to generate questions and hunches that later research can pin down. It is typically small-scale and open-ended, relying on informal conversations, open interviews, and observation. Its characteristic output is not an answer but a better set of questions. At Meridian, where nobody yet knows why people leave, open-ended exit conversations with recent leavers — conducted before any questionnaire is written — are exploration.
Descriptive research
Descriptive research answers the questions what, who, where, when, how many, how often — precisely and systematically. It measures and reports the characteristics of a population or situation: how turnover is distributed across stores, roles, tenure bands, and age groups; what satisfaction scores look like month by month and channel by channel. Careful description is not a lesser form of research; it is the foundation on which everything else stands, and the warning from session 1 applies directly — we cannot explain what we have not first described accurately. For Meridian, answering “which stores, roles, and tenure groups have the highest turnover?” tells the board where the problem lives, though not yet why.
Explanatory research
Explanatory research answers the question why. It seeks the causes, reasons, and mechanisms behind what description has established, typically by relating variables to one another: does workload drive resignations? Does store-level management quality? Does pay relative to local competitors? Explanation is the most ambitious of the three goals, because establishing cause in the social world is genuinely difficult — many things vary at once. It is also the goal managers usually care about most, because causes are levers: only when you know why something happens can you sensibly intervene. “Does perceived workload explain why sales staff resign?” is an explanatory question; if the answer is yes, the board has something it can act on.
Goals combine and sequence
Real projects rarely serve a single goal. The three typically form a sequence: explore to find out what might matter, describe to establish the pattern precisely, and explain to test why the pattern holds. A single study can serve more than one goal, but every study should know its primary goal, because that is what disciplines the design. Mislabelling the goal is a genuine failure mode: an exploratory study dressed up as explanation over-claims, while an explanatory question tackled with exploratory tools under-delivers. Meridian’s project runs through all three goals in order: exit conversations (exploration), a turnover audit (description), and then a test of the workload hypothesis (explanation).
Figure 4 draws the sequence as three chevrons, with Meridian’s project under each — exit conversations, a turnover audit, a test of the workload hypothesis — and the two ways of mislabelling a goal underneath.
From topic to research question
Why research questions matter
A topic tells you what territory you are in; a research question tells you what, exactly, you must find out. The research question does three jobs at once: it guides the research, since every later decision refers back to it; it determines the scope of the study, fixing what falls inside and outside; and it shapes the choice of methodology, since the wording of a question points toward the methods capable of answering it. A study without a clear question drifts — data get collected because they are available rather than because they are needed. The question is the heart of the study; everything else is anatomy arranged around it.
Types of research question
Each research goal has characteristic question forms:
| Type | Asks | Goal served |
|---|---|---|
| Descriptive | What is happening? How much? How often? | Description |
| Comparative | How do A and B differ? | Description |
| Explanatory | Why is X happening? Does X affect Y? | Explanation |
| Exploratory | What could be going on here? What might matter? | Exploration |
Comparative questions are description with a sharper edge: comparing groups is often the first step toward explaining the differences between them. The type of question is a commitment — it tells the reader what kind of answer to expect.
Applied to a single topic — voluntary resignations at Meridian — the four types yield four different studies:
- Exploratory: What do departing employees say about their reasons for leaving Meridian?
- Descriptive: How does voluntary turnover vary across Meridian’s stores, roles, and tenure bands?
- Comparative: Do turnover rates differ between Meridian’s stores and its e-commerce arm?
- Explanatory: Does perceived workload affect front-line employees’ intention to quit?
Same company, same problem — but four different kinds of evidence, and four different things the board would learn. Choosing among them is not a technicality.
Figure 5 shows the same four questions as branches of one topic, each tagged with the kind of evidence it calls for.
Managerial questions and research questions
Managers ask questions like how do we stop people leaving? Such questions are legitimate and urgent, but they are not researchable as stated. A managerial question is a demand for a decision; a research question is a demand for knowledge. The translation between them runs in both directions. Downward, the decision is broken into the pieces of knowledge it depends on: who leaves? why? what would retain them? Upward, research answers feed back into the decision — but the decision itself also weighs costs, values, and strategy, which research can inform but cannot settle. “Should we raise pay?” is a decision question; “would a pay rise reduce resignations more than a workload reduction?” is a research question. In practice, a research team’s first deliverable is often not data at all, but the translation of a client’s worry into three or four researchable questions.
Figure 6 traces the translation. The managerial question is broken down into research questions; their answers inform the decision, which also weighs costs, values and strategy; and the same issue can be posed both ways — “should we raise pay?” as a decision, “would a pay rise reduce resignations more than a workload reduction?” as research.
Criteria and common flaws
Criteria for a sound research question
This course works with four criteria. A sound research question is:
| Criterion | Test |
|---|---|
| Answerable | Evidence could in principle settle it; you can say what data would count as an answer |
| Focused | It asks one thing, about a defined population, place, and period |
| Feasible | It can be answered with the time, access, skills, and resources actually available |
| Non-trivial | The answer is not already known or true by definition; someone learns something |
Textbook lists add further virtues — clear and concise, researchable, relevant and significant, specific and focused, original — but these are the same qualities viewed from different angles. The sharpest single test is: can I describe the evidence that would answer this question, and could that evidence realistically be gathered?
Figure 7 draws the four criteria as gates a question must pass in turn, each with its test, and the sharpest single test underneath.
Common flaws
Eight flaws account for most bad research questions. Each is a failure against one or more of the four criteria, and each has a standard repair.
| Flaw | What goes wrong | Example | Repair |
|---|---|---|---|
| Too broad | The question covers a field, not a study | “What affects employee motivation?” | Narrow by aspect, component, type, place, time, or relationship |
| Unanswerable | No evidence could settle it, even in principle — bare counterfactuals, essentialist questions | “Would turnover have stayed at 14% without the e-commerce expansion?” | Rebuild around something observable: a comparison, a measurable outcome, a defined population |
| Double-barrelled | One question smuggles in two, which may have different answers | “How satisfied are employees with their pay and their line managers?” | Split it; ask each question separately |
| Leading | The question presupposes the answer to the thing at issue | “Why do Meridian’s store managers neglect their staff?” | Remove the presupposition: first ask whether, then ask why |
| Value-laden | It asks for a moral verdict, not an empirical finding | “Is it acceptable for Meridian to monitor employees’ screen activity?” | Research the empirical parts (effects on trust, stress, performance); leave the verdict to deliberation informed by the evidence |
| Trivial | Answerable, focused, feasible — and worthless, because the answer is already known | “Do employees prefer being paid on time to being paid late?” | Find the version whose answer is genuinely uncertain |
| Not researchable | A decision or policy question posed as empirical — “should” mixes evidence with strategy, cost, and values | “Should Meridian close its five worst-performing stores?” | Extract the researchable core, e.g. how much of the underperformance closure would actually fix |
| Prediction without mechanism | A bare forecast with no explanatory content — nothing learned transfers | “Will customer satisfaction improve next year?” | Anchor the prediction in a mechanism, e.g. whether delivery speed drives satisfaction |
Two remarks are worth adding. First, the double-barrelled and leading flaws recur, in identical form, in questionnaire wording — spotting them now pays off again when we design surveys later in the course. Second, note the asymmetry between the value-laden and trivial flaws: the former asks too much of research, the latter too little.
Figures 8 to 11 take the flaws in pairs, as the slides do. Each card gives the definition, a flawed example (in the red box), why it fails, and the repair (in green).
Conclusion
Research starts before data. The journey from a managerial problem to a researchable question is itself methodological work, and it is where most studies are won or lost. A good topic passes the tests of relevance, feasibility, and practicality, and sits at the right scope — neither a whole field nor a one-off incident. Every study serves a goal — exploration, description, or explanation — and the goal disciplines the question: what could be going on, what is happening, why is it happening. Sound research questions are answerable, focused, feasible, and non-trivial, and the eight common flaws — double-barrelled, leading, value-laden, unanswerable, too broad, trivial, unresearchable, and mechanism-free prediction — are all failures against one of those four criteria. The next session takes the step this one deliberately stopped short of: turning research questions into hypotheses and variables, and choosing a research design to test them.