Somewhere in every department there is an unofficial graveyard. It isn't a place, exactly - more a set of phrases that make supervisors' faces do something complicated when they hear them in a first meeting. "I want to look at the effect of social media on society." "I'm interested in why people commit crime." "My dissertation will be about whether AI is going to replace lawyers." The supervisor's expression isn't contempt. It's recognition. They have seen this topic before, they know it will not survive in its current form, and they are working out how to say so without extinguishing the genuine curiosity that produced it.
Because that's the thing about the topics in the graveyard: they are almost all good ideas. They are interesting, important, and often exactly the questions that drew the student into their subject in the first place. The problem is never the interest. The problem is that an interest is not a research question, and the gap between the two is where dissertations go to die - usually around month four, when the student discovers that "society" cannot be sampled and "success" cannot be measured.
In the previous article in this series we looked at research plans that collapse under the question "how would you do that?" - access, ethics, time, cost, data and method. This piece steps back one stage further, to the topic itself: the ideas that fail before there's anything to plan, because they are too broad, impossible to evidence, dependent on data no one will release, built around a conclusion already reached, or simply the size of a career rather than a year. Seven headstones follow. For each: why the idea is appealing, what killed it, and - most importantly - the smaller, sharper, living question that was hiding inside it all along.
Why the graveyard fills up
The pattern is so consistent that it's worth understanding before the examples. Wayne Booth, Gregory Colomb and Joseph Williams, in The Craft of Research - probably the most widely assigned book on the subject - describe the journey from topic to question to problem: a topic is what you're interested in, a question is something specific you don't know about it, and a problem is why anyone else should care about the answer. Their diagnostic sentence has rescued countless proposals: "I am studying ______ because I want to find out ______ in order to help my reader understand ______." Graveyard topics fail because the student has filled in only the first blank. "I am studying social media and society" is a topic. There is no second blank, and therefore nothing to research.
Why do bright students stop at the first blank? Partly because school and undergraduate assessment never asked them to fill in the others - a point we've made about the dissertation transition generally in our article on what supervisors really mean. But partly because broad topics feel safer. A big question seems to guarantee there'll be enough to say; a narrow one seems to risk running out. The reality is the reverse. Broad topics produce dissertations that skate across the surface of a hundred sources without adding anything, and examiners can spot them in the first page. Narrow questions produce depth, and depth is what gets marked. As the old research adage goes: you can say something about everything or everything about something, and only one of those is a dissertation.
Seven headstones
1. "The effect of social media on society"
Why it's appealing: It's arguably the defining social question of the age, it's personally relevant to every student, and the literature is enormous, so there's clearly something to work with.
Cause of death: every noun is undefined. Which social media - a broadcast platform like YouTube, a messaging service like WhatsApp, a feed-driven network like TikTok? These have almost nothing in common as technologies or experiences. Which effect - on mental health, political polarisation, attention, friendship, sleep, commerce, language? Which society - a 19-year-old in Manchester, a farmer in Kenya, a pensioner in Osaka? Each dimension left open multiplies the project until it isn't one. And the field is not a settled body of knowledge waiting to be summarised; it's a live, bitter dispute among specialists with vast datasets. When Jonathan Haidt's The Anxious Generation argued in 2024 that smartphones had "rewired" adolescence, the developmental psychologist Candice Odgers replied in Nature that the evidence for a causal effect on mental health was not there - and these are two experts drawing on hundreds of studies and reaching opposite conclusions. A student with nine months and no data cannot adjudicate a debate that the people with all the data haven't resolved.
What could have lived: Fix each noun. "How do final-year undergraduates at one UK university describe using Instagram's 'close friends' feature to manage self-presentation during job applications?" Platform, feature, population, behaviour, context - all specified. Or, for a quantitative version, one association in one population with one validated measure, honestly framed as association. The topic is the same; the question is now answerable.
2. "Why people commit crime"
Why it's appealing: It's the foundational question of an entire discipline, and it sits at the intersection of psychology, sociology, economics and policy. Answer it and you'd change the world.
Cause of death: it is the discipline. Criminology has been trying to answer this since Beccaria in 1764 and Lombroso in the 1870s. Merton's strain theory, Sutherland's differential association, Hirschi's social control theory, Gottfredson and Hirschi's general theory, Sampson and Laub's life-course perspective - each is a career-long research programme, and they disagree. Consider the scale of effort involved in even a partial answer. The Cambridge Study in Delinquent Development has followed 411 London boys, first assessed at age eight in 1961, through nine rounds of interviews and criminal-record searches up to age 61 - a research programme spanning six decades and multiple generations of researchers. It has found that 44% were convicted at some point, that childhood factors such as harsh parental discipline, poor supervision and a convicted father predicted long criminal careers, and that offending typically results from "a combination of childhood adversities." Even after sixty years, its authors are careful to note it describes one cohort of working-class white males from inner London born around 1953, and that generalisation is "an interesting empirical question." That is what an honest answer to "why people commit crime" looks like: sixty years, one population, and caveats. A dissertation cannot compete with that, and shouldn't try.
What could have lived: Pick one theory, one population, one mechanism. "Does Hirschi's concept of attachment explain differences in self-reported minor offending among first-year university students?" Or go qualitative on one pathway: how do people who desisted from offending in their twenties narrate the turning point? Both engage the grand question through a keyhole - which is how every criminologist actually works.
3. "Whether AI will replace lawyers"
Why it's appealing: It's topical, career-relevant for every law student, and a genuine source of anxiety and excitement in the profession.
Cause of death: you cannot collect evidence about the future. A dissertation is an empirical or analytical exercise; a prediction is a bet. The record of expert forecasting on questions like this is sobering. Philip Tetlock's twenty-year study of political and economic experts - 284 forecasters, roughly 28,000 predictions - found that on long-range questions specialists performed scarcely better than what he memorably called a "dart-throwing chimpanzee." In this exact domain, the range of expert estimates is a warning in itself: Frey and Osborne's much-cited 2013 Oxford study put 47% of US jobs at "high risk" of automation, while Dana Remus and Frank Levy's detailed analysis of actual law-firm billing data estimated that automation might reduce demand for lawyers' hours by around 13% - spread over years - because "legal analysis and strategy" alone accounts for 28% of billable time and is precisely what machines do worst. If the experts span 13% to 47% using the best data available, a student cannot settle it, and a dissertation that tries will end up as a literature summary with a guess attached.
What could have lived: Move the tense from future to present. Remus and Levy's own method is the model: what proportion of specific legal tasks is currently being performed with AI assistance in a defined set of firms, and how do trainees describe the effect on their work? Or study the regulation as it exists - how the SRA and Bar Standards Board have responded to generative AI. Or analyse the discourse: how has the profession's own press framed automation over ten years? Every version produces evidence rather than prophecy.
4. "How to solve climate change"
Why it's appealing: It matters more than almost anything else, and students who care about it - rightly - want their work to count.
Cause of death: it isn't a question, it's a mission - and a "wicked" one. In a landmark 1973 paper, the planning theorists Horst Rittel and Melvin Webber distinguished tame problems, which have definable solutions, from wicked problems, which have no definitive formulation, no stopping rule, no right-or-wrong test, and where every attempted solution changes the problem. Climate change is the canonical wicked problem: scientific, economic, political, ethical and technological at once, with no single "solve." Consider the scale of the institution that exists to summarise what's known: the IPCC's Sixth Assessment Report's physical-science volume alone runs to nearly 4,000 pages, was written by more than 230 authors, and cites over 14,000 studies - and it is a summary, of one strand, offering no policy prescriptions. "How to solve climate change" is a topic the size of a civilisation.
What could have lived: One intervention, one place, one measurable outcome. "Did the introduction of a Clean Air Zone in Birmingham change commuting mode choices among city-centre workers?" "How do UK farmers in one region perceive the barriers to adopting agroforestry payments?" "What explains variation in heat-pump uptake across English local authorities?" Each contributes a brick. Climate research, like criminology, is built entirely of bricks; nobody hands in the cathedral.
5. "The impact of leadership on business success"
Why it's appealing: It's the most-read topic in business, every MBA course touches it, and the case studies are compelling. Surely leadership matters?
Cause of death: circularity, contaminated evidence, and two undefined terms. Start with definitions. "Leadership" spans dozens of constructs - transformational, servant, authentic, transactional, distributed - measured by competing instruments. "Success" could be share price, profit, growth, survival, employee wellbeing or reputation, and these frequently point in different directions. But the deeper problem is that our judgements about leadership are largely caused by our knowledge of performance, not the other way round. In a classic 1975 experiment, Barry Staw told groups of participants - at random - that they had performed well or badly on a task; those told they'd succeeded then recalled their group as more cohesive, better at communicating and more open to change, though the groups had performed identically. James Meindl's research on the "romance of leadership" found the same for leaders: descriptions of a CEO's vision or arrogance track the company's results, not any stable trait. Phil Rosenzweig's analysis of this halo effect showed how it undermines even famous large-scale studies: Jim Collins's Good to Great selected its eleven "great" companies by outcome and then explained their greatness largely from press coverage and retrospective interviews - sources already glowing with the halo. Two of the eleven, Circuit City and Fannie Mae, subsequently went bankrupt or into government conservatorship. A student who interviews managers about "what leadership made your firm successful" will collect exactly the same contaminated data, and reach exactly the same unfalsifiable conclusions.
What could have lived: One defined leadership construct, one outcome measured independently of anyone's opinion of the leader, and data collected without knowledge of results. "Is the frequency of documented one-to-one meetings between line managers and staff associated with team retention rates in one retail chain?" Or turn the halo effect itself into the study: how did press descriptions of a named CEO change before and after a share-price fall, holding the leader constant? That's a genuinely publishable question, and the data is public.
6. "Why patient safety incidents happen on my ward"
Why it's appealing: For a nursing or healthcare student, it's the most authentic topic possible - real, urgent, and rooted in first-hand experience.
Cause of death: the data is confidential, and the ethics are institutional, not personal. Any study touching NHS patients, records or incident reports requires approval from the Health Research Authority and usually an NHS Research Ethics Committee - a process that takes months and typically requires a sponsor, which student projects rarely have. Incident reports contain identifiable patient information and staff details that no trust will release to a student. Interviewing colleagues about safety failures on a ward where you work raises further issues of confidentiality, power and the possibility of surfacing reportable incidents you would then be obliged to act on. None of this means the topic is illegitimate; it means it belongs to a different scale of research infrastructure than a dissertation possesses. Students who start here often spend their entire data-collection window inside an approval process and finish with nothing.
What could have lived: Use what's already public. National patient-safety incident data is published in aggregate; the NHS Staff Survey releases trust-level results on "raising concerns" and safety culture every year; Care Quality Commission reports describe safety issues in detail. "How does reported safety culture in the NHS Staff Survey vary between trusts with different staffing ratios?" needs no ethics approval and answers a version of the question. Alternatively, a rigorous literature review or a study of student nurses' perceptions of speaking-up culture - your own peer group, approvable through a university committee - keeps the topic and sheds the barriers.
7. "Why remote working is better for productivity"
Why it's appealing: It's current, it's contested, and the student - probably a remote worker themselves - has a view.
Cause of death: the conclusion is in the title. A research question must be capable of coming out the other way; Karl Popper's insistence on falsifiability is the difference between inquiry and advocacy. "Why remote working is better" has already decided the answer and is looking for supporting material - and the human mind is spectacularly good at finding it. Peter Wason's 1960 experiments showed people testing a hypothesised number rule almost exclusively by generating examples that confirmed it, rarely attempting the disconfirming test that would have revealed their error; Raymond Nickerson's 1998 review concluded that this confirmation bias is among the most robust findings in psychology. A student who has pre-decided will read the mixed evidence selectively - and the evidence here is mixed: Nicholas Bloom's 2015 randomised trial at a Chinese travel firm found a 13% productivity gain from home working, while his 2024 study of hybrid working in Nature found no significant difference in performance but a large fall in resignations. A dissertation that reports only the 13% is not research. Examiners, who know the literature, will read it as a position paper.
What could have lived: Open the question so that "no" is a possible answer, and define the terms. "How does the number of days worked remotely relate to self-reported task completion and collaboration quality among software developers in one company?" - with the explicit acknowledgement that the association may be zero or negative. The moment you can say what result would surprise you, you have a research question.
The anatomy of a question that survives
Lay the seven resurrected questions side by side and the pattern is unmistakable. Every living question has been constrained along the same handful of dimensions. Before committing to any topic, run it through them:
- Population: Who or what, precisely? Not "people" or "businesses" but "final-year undergraduates at one university," "SMEs in the Yorkshire food sector," "English local authorities."
- Place and period: Where, and when? A defined setting and time window converts a universal claim into a study.
- Variable or mechanism: Which specific feature of the broad phenomenon? Not "social media" but one platform feature; not "leadership" but one measurable behaviour.
- Outcome: What exactly will you measure or describe, and could it be measured independently of anyone's opinion about the cause?
- Direction: Is the question genuinely open? Could the answer be "no," "none," or "the opposite" - and would you report that?
- Tense: Is it about something that exists or has happened, rather than something that might?
- Contribution: Booth's third blank - who needs to understand this, and what changes if they do? A question can be perfectly specified and still not matter.
Notice that the FINER criteria we discussed in the previous article - feasible, interesting, novel, ethical, relevant - are judged after this step. You cannot assess the feasibility of "the effect of social media on society" because there is nothing specific enough to assess. Scoping comes first; feasibility second; the plan third.
Notice also that narrowing is not a loss of ambition. Every one of the seven resurrected questions still speaks to the grand topic that motivated it - the student who studies Instagram's close-friends feature is studying social media and society; the student who studies desistance narratives is studying why people commit crime. The introduction and discussion chapters are where you connect the brick to the cathedral. The methods chapter is where you lay the brick. Confusing the two is how topics end up in the graveyard.
Titles are compressed questions
One practical consequence is often overlooked: a dissertation title is a research question with the grammar removed, and a title that cannot be expanded back into a specific question is a warning sign. Compare the graveyard versions with what a living title looks like:
- "The effect of social media on society" → "Curating the audience: how final-year undergraduates use Instagram's 'close friends' feature during the graduate job search"
- "The impact of leadership on business success" → "Meeting frequency and staff retention: line-manager contact and turnover in a UK retail chain, 2023–2025"
- "Whether AI will replace lawyers" → "Automation at the task level: how trainee solicitors in three City firms describe generative AI in due diligence work"
The living titles are longer, more specific and less grand - and every one of them tells an examiner, before they've read a word of the abstract, that the author knows what a research question is. That impression is worth marks.
Where to get help choosing - and why it's legitimate to ask
Students often assume that choosing a topic is the one part of the dissertation they must do entirely alone, as though asking for help at this stage were somehow cheating at the starting line. The opposite is true: topic selection is the stage at which experienced input has the highest possible return, because a badly scoped topic wastes months and a well-scoped one saves them. Supervisors expect to help here - most will happily take a graveyard topic and talk you towards a living one, and "here are three broad interests, which has legs?" is a perfectly good opening for a first meeting. Reading recent dissertations in your department's repository shows you the actual grain size of successful projects. Subject librarians can tell you in twenty minutes whether a topic has a literature large enough to review but small enough to master. And recent journal articles almost always end with a "directions for future research" paragraph, which is a list of pre-scoped, examiner-approved questions hiding in plain sight.
Beyond the university, specialist topic-and-title support fills a specific gap: many students know their broad interest but have never seen enough well-formed research questions in their own field to recognise the shape of one. Being shown a set of properly scoped, feasible candidate titles - with a rationale for each, written by an academic who knows where the genuine gaps in the literature are and what can realistically be done in nine months - is exactly the kind of worked example this series keeps returning to. UKEssays' dissertation topic and title service does precisely that: it takes a broad interest and returns researchable options, so you can see how "leadership and success" becomes a question with a population, a variable and a measurable outcome. As always, the model is there to be learned from and made your own: adapt the scope, shift the population to one you can actually reach, sharpen the angle to the thing you genuinely want to know. The topic you finally choose has to be yours - you're the one who'll live with it for the best part of a year, and the project will only be good if the question keeps you curious in month seven. But there is no virtue in spending your first six weeks reinventing what an experienced researcher could show you in an afternoon.
The bottom line
The dissertation topic graveyard is not full of bad ideas. It's full of good interests that were never turned into questions - topics with every noun undefined, conclusions already reached, futures that can't be evidenced, data that can't be obtained, and problems the size of whole disciplines. The way out is not to care less about the big questions but to understand how big questions are actually answered: one specified population, one defined variable, one measurable outcome, one honest direction at a time. The Cambridge study took sixty years and 411 boys to say something careful about crime. The IPCC took 4,000 pages to summarise one strand of climate science. Nobody expects your dissertation to do either. They expect you to find the brick that's yours, describe it precisely, lay it well, and explain in your introduction which cathedral it belongs to. Do that, and the topic that sounded impossibly broad in your first supervision meeting becomes the project that finishes - and finishing, as every supervisor will tell you, is the single most underrated quality in a research question.
