Every supervisor knows the moment. A student arrives with an idea they've clearly been turning over for weeks - eyes bright, notes ready - and it is a good idea. It's interesting. It matters. It would make a genuinely valuable contribution if it existed. The supervisor listens, nods, and then asks the question that quietly ends about half of all dissertation proposals in their first form:
"And how, exactly, would you do that?"
What follows is one of the most useful conversations in a research education, and also one of the most deflating. Because "how would you do that" isn't one question - it's six, and a project must survive all of them. Who will give you access? Will an ethics committee allow it? Can you finish in the time you have? Can you afford it? Does the data actually exist? And does the method you've chosen have any hope of answering the question you've asked? Most brilliant-sounding ideas fail at least one. The good news is that very few need to be abandoned. They need to be redesigned, and the skill of redesigning an ambitious idea into a workable plan is, arguably, the single most transferable thing a dissertation teaches.
This article walks through six plausible student projects - each fascinating, each fatally flawed as first proposed - and shows where the collapse happens and what the idea can become instead. Along the way it draws on the evidence about why researchers, even professional ones, so reliably overestimate what they can do.
Why smart people propose impossible projects
Before the case studies, one piece of context, because it removes the shame. Overambitious research plans aren't a student failing; they're a human one. In a now-classic 1994 study, psychologists Roger Buehler, Dale Griffin and Michael Ross asked honours students at the University of Waterloo to predict when they would submit their thesis. On average, students predicted 33.9 days. They actually took 55.5. Fewer than a third (29.7%) finished by their own "most accurate" estimate - and even when asked to imagine everything going as badly as it possibly could, their pessimistic guess of 48.6 days still undershot reality. The researchers named this the planning fallacy: people plan from an imagined scenario in which things go smoothly, rather than from their own track record of things not going smoothly.
The same optimism infects every dimension of a research plan, not just time. We imagine the executive replying to the email, the ethics committee waving the study through, the company handing over the spreadsheet, the twenty participants turning up. The proposal stage exists to replace those imagined scenarios with evidence. Clinical researchers, who have measured this carefully, provide a sobering benchmark: a review of 114 UK-funded trials found that fewer than a third recruited their target number of participants on schedule, and over half needed extensions - and these were funded, experienced teams with dedicated staff. If professionals miss by that margin, a student's plan should be built with a wide safety margin by default.
Six projects that sounded brilliant
1. "I'll interview FTSE 100 chief executives about leadership in a crisis"
Why it sounds brilliant: Elite decision-making under pressure is a genuinely important and under-studied topic. First-hand accounts from people who've actually run large organisations through a crisis would be gold.
Where it collapses: Access. The single most reliable predictor of whether an elite interview happens is a pre-existing relationship, and undergraduates and master's students almost never have one. The evidence here is stark. Cheryl Cycyota and David Harrison's meta-analysis of 231 published studies that surveyed executives - studies run by established academics, often with institutional or professional-association sponsorship - found an average response rate of just 32%, and falling over time. Their central finding was that the usual response-boosting techniques (incentives, follow-ups, personalisation) barely worked with executives; what worked was sponsorship by someone already in the executive's network. A student cold-emailing a corporate communications inbox is not in that network. A realistic expected yield from fifty such emails is somewhere between zero and two interviews - and a qualitative study needs, as we'll see, around a dozen.
What it can become: The question survives; the population changes. Interview middle managers who implemented crisis decisions - far more numerous, far more reachable through alumni networks and LinkedIn, and arguably more revealing about how leadership actually lands. Or move from people to documents: CEO letters in annual reports, earnings-call transcripts, published interviews and parliamentary select-committee testimony are all public, abundant and analysable, and elite-discourse analysis is a respected method in its own right. Or study a single organisation where you have a genuine connection - a placement employer, a family business, a university's own senior team - and go deep rather than wide.
2. "I'll observe street-level drug dealing to understand the informal economy"
Why it sounds brilliant: Illicit markets are economically significant, sociologically rich and hard to study - which is exactly why there's a gap in the literature. Ethnography of hidden worlds has produced some of the most celebrated work in the social sciences.
Where it collapses: Ethics and safety, immediately and completely. No university ethics committee will approve a student directly observing criminal activity, and the reasons are not bureaucratic timidity. Consider what the committee has to weigh: risk to participants (people whose behaviour you record could face serious consequences if your data were ever seen by anyone else, and you cannot guarantee it won't be); risk to the researcher (physical danger, and the possibility of being drawn into or witnessing harm with no protocol for what to do next); and the impossibility of meaningful informed consent in covert observation. The celebrated studies students cite as precedent are actually cautionary tales. Laud Humphreys' 1970 Tearoom Trade, which covertly observed men in public toilets and then traced their home addresses via licence plates, is taught today primarily as an example of what research ethics was created to prevent. Sudhir Venkatesh's Gang Leader for a Day, based on years embedded with a Chicago gang as a doctoral student, is a gripping read - and Venkatesh himself has described the ethical tangles it created, including knowledge of planned crimes and a research design that would not pass a modern review board.
What it can become: Change the vantage point. Interview people with past involvement, recruited through a gatekeeper organisation (a drugs charity, a rehabilitation service, a probation-linked programme) that already has safeguarding structures - still demanding, but approvable with care. Analyse sentencing remarks and court judgments, which are public and describe informal markets in remarkable detail. Use the Crime Survey for England and Wales or other secondary datasets. Or study the policy debate: how the informal economy is framed by legislators, media and enforcement agencies. Every one of these answers a version of the original question without putting anyone in a cell or a hospital.
3. "I'll prove social media causes anxiety by surveying ten of my friends"
Why it sounds brilliant: It's a live public question, personally relevant, and a survey feels achievable. Everybody has an opinion about this.
Where it collapses: Methodological fit - in three separate ways. First, the word prove. Research does not prove; it provides evidence of varying strength. Second, the word causes. A one-off survey is cross-sectional: it measures social-media use and anxiety at the same moment, so it cannot tell you which came first. Anxious people might use social media more (reverse causation); a third factor - sleep, loneliness, exam season - might drive both (confounding). Establishing causation requires a design that handles time and confounders: a longitudinal panel, a natural experiment, or a randomised intervention. None is available to a ten-person survey.
Third, the number ten. With ten participants, the smallest correlation you could detect as statistically significant is about r = 0.63 - an enormous effect, far bigger than almost anything in social science. Jacob Cohen's standard power tables show that detecting even a medium effect between two groups with conventional 80% power needs about 64 people per group; a small effect needs nearly 400 per group. And the actual effect in this literature is small: Amy Orben and Andrew Przybylski's 2019 analysis of over 350,000 adolescents found digital technology use explained at most 0.4% of the variation in wellbeing - an association about the size of that between wellbeing and wearing glasses or eating potatoes. A ten-person survey has no chance of detecting an effect that size; whatever it "finds" will be noise, and a marker will say so.
What it can become: Match ambition to method. Ask an association question, not a causal one, in a defined population, with a sample size justified by a power calculation - or, better, use existing large datasets (the Millennium Cohort Study, Understanding Society) which track thousands of people over years and are free to registered students. Alternatively, go qualitative: a dozen in-depth interviews about how students experience the relationship between their online lives and their moods can generate genuine insight, precisely because it doesn't pretend to measure a population effect.
4. "My placement company has promised me their customer data"
Why it sounds brilliant: Real commercial data is exactly what most student projects lack, and a friendly manager said yes.
Where it collapses: Data availability - specifically, the gap between what an enthusiastic individual promises and what an organisation will actually release. The manager who said yes in June is not the person who decides in October; that person sits in data protection, legal or compliance, and their default answer to "can a student have our customer records for a dissertation?" is no. Even when data is released, it's frequently anonymised or aggregated to the point where the planned analysis is impossible, arrives months late, or comes with confidentiality conditions that prevent you reporting what you found. Projects built entirely on a single external data promise fail at a rate that experienced supervisors describe as routine.
A close cousin is the policy-evaluation project: "I'll assess whether last year's government scheme worked." The scheme may be a year old, but official outcome statistics typically lag by twelve to twenty-four months, so the data that would answer the question won't exist until after your deadline.
What it can become: Never build on a single point of failure. Secure the data in writing, before the proposal is approved, with a named owner and a date - and design a fallback that uses public sources: Companies House filings, annual reports, ONS datasets, the UK Data Service (which holds thousands of curated datasets available to students), publicly available review data, or trade-body statistics. For the policy project, evaluate an older scheme whose data has matured, or study implementation and stakeholder experience rather than outcomes. A dissertation with a Plan B is not less ambitious; it's more professional.
5. "I'll follow first-year students' wellbeing across the whole academic year"
Why it sounds brilliant: Longitudinal designs are exactly what's needed to study change - and, as case three showed, they're what causal questions demand.
Where it collapses: Time, on three fronts at once. First, arithmetic: a "whole academic year" of data collection cannot fit inside a nine-month dissertation that also needs a literature review before and analysis and writing after. Second, ethics lag: a study of student wellbeing will need approval, which typically takes weeks at a university committee (and months for anything involving the NHS), so your "September" first wave becomes November at best. Third, attrition: longitudinal studies routinely lose 20–50% of participants between waves; a project starting with 40 and ending with 18 has a very different analysis from the one you planned. Layer the planning fallacy over all of that - remember the pessimistic estimate that was still too optimistic - and the year-long study is a dissertation that gets written in a panic with half its data.
What it can become: Shrink the window. A two-wave design over eight weeks (say, before and after the first assessment period) is a genuinely longitudinal design that fits the calendar. Or ask the same question retrospectively - interviewing second-years about their first year - accepting recall limitations and discussing them honestly. Or, once again, lean on the giants: national longitudinal datasets already follow tens of thousands of young people through education, and secondary analysis of them is a fully legitimate dissertation.
6. "I'll do forty interviews, a national survey and a document analysis"
Why it sounds brilliant: Mixed methods are fashionable, triangulation sounds rigorous, and more data feels safer.
Where it collapses: Cost and scope, measured in hours. Start with the interviews. Forty one-hour interviews means, at a conservative four hours of transcription per recorded hour, 160 hours of typing before analysis begins - that's a month of full-time work, on transcription alone. Then the analysis: proper qualitative coding of forty transcripts is a further several weeks. And the effort is largely wasted, because you didn't need forty. Monique Hennink and Bonnie Kaiser's 2022 systematic review of empirical tests of saturation found that studies with reasonably focused questions and populations reached saturation at 9–17 interviews, with a mean of 12–13 - consistent with Guest and colleagues' landmark 2006 finding of saturation at twelve. Beyond that point, additional interviews generate diminishing new themes at undiminished cost. Add a national survey (which needs sampling strategy, instrument design, piloting and a panel provider you likely can't afford) and a document analysis, and you've proposed three dissertations, each of which will be done worse than one would have been.
What it can become: One method, executed excellently. Twelve to fifteen well-conducted interviews with a coherent population, analysed rigorously and written up with methodological self-awareness, will outscore a sprawling three-strand project every time - because examiners mark depth, coherence and justification, not volume. If triangulation genuinely matters to the question, keep the secondary strand tiny: a brief document review to contextualise the interviews, not a parallel study.
The six questions every idea must survive
Notice the pattern. Each project failed on one axis while being perfectly sound on the others - which is why the feasibility check needs to be systematic rather than intuitive. Clinical researchers formalised this decades ago as the FINER criteria (Hulley and colleagues, Designing Clinical Research): a good research question must be Feasible, Interesting, Novel, Ethical and Relevant. Students almost always nail I, N and R. It's F and E that kill projects. Expanding "feasible" into its components, run every idea through these before you fall in love with it:
- Access: Who, specifically, will give you the people or the data - and have they said so in writing? If your plan depends on strangers replying to emails, assume a single-digit response rate.
- Ethics: Could this harm participants or you? Does it involve vulnerable groups, deception, covert observation, sensitive topics or minors? Each is possible, but each adds weeks and may be off-limits at your level.
- Time: Map the calendar backwards from submission, subtracting writing, analysis, ethics approval and a recruitment period at least twice as long as you first guessed. What data collection window actually remains?
- Cost: Count hours as well as pounds. Transcription, travel, incentives, software, survey panels - and your own labour, which is finite.
- Data availability: Does the data exist, is it accessible to you, is it in a usable form, and will it exist in time? If the answer to any part is "probably," you need a Plan B.
- Methodological fit: Can this method, at this scale, answer this question? Causal questions need designs that handle time and confounding; "how do people experience" questions need qualitative depth; population claims need samples sized to detect the effect you expect.
The management scholars Amy Edmondson and Stacy McManus have a useful name for the sixth test: methodological fit - the internal consistency between your question, the maturity of existing theory, your methods and your contribution. Their key insight is that misfit doesn't just weaken a project; it makes the findings uninterpretable, because you cannot tell whether a null result reflects reality or a method that never had a chance. Fit is the difference between "I found nothing" and "I could not have found anything."
The proposal: where an idea has to become a plan
All of this is why the research proposal exists - and why students who treat it as a formality to get past, rather than the most important document of the project, tend to be the ones writing panicked emails in month seven. A proposal is the formal moment when "wouldn't it be fascinating to…" must become "here is exactly how, with whom, by when, and why this method answers this question." Its standard components - research question, literature rationale, methodology and justification, sampling and access strategy, ethical considerations, timeline, and (often) a risk register - map almost one-to-one onto the six feasibility tests above. A proposal that has genuinely been worked through is the feasibility check. That's its function.
Two practical implications follow. First, the timeline in your proposal should be built against the planning-fallacy evidence, not against hope: take your honest estimate for each stage and add the margin that Buehler's students needed - around 50% - then add contingency for the one thing you haven't thought of, because there is always one. Second, write the risk register seriously. "Company data may not be released - fallback: UK Data Service dataset X" is not an admission of weakness; it's exactly the kind of thinking examiners reward and the one thing that separates projects that finish from projects that stall.
Many students find the proposal genre itself unfamiliar - it's the first document they've written that argues for a plan rather than about a topic, and the conventions (how a methodology is justified rather than described, what a defensible sampling rationale looks like, how a timeline and risk assessment are laid out) are rarely taught explicitly. The approach we've recommended throughout this series applies directly: study a well-constructed example of the genre before writing your own. Seeing a rigorous proposal - how it moves from question to method to feasibility, how it pre-empts the "how would you do that" question in every section - shows you the standard concretely. Specialist support such as UKEssays' research proposal service provides model proposals written by academics who know what supervisors and ethics committees look for, and feedback on your own draft before it goes to your department. Used as intended - learn how a workable plan is constructed, then build your own around your own question and constraints - it's a way of borrowing an experienced researcher's feasibility instincts before you've developed your own. The usual rule holds: it's a scaffold to learn from, and the proposal you submit must be yours, because the project it describes is one only you will have to live with for the next nine months.
Rescue, don't abandon: the scaling ladder
The most important lesson from the six cases is that not one of them needed to be thrown away. Each was rescued by moving one rung on what might be called the scaling ladder - a set of standard moves for turning an infeasible idea into a feasible one while preserving what made it interesting:
- Same question, narrower population. Not FTSE CEOs but middle managers in one sector; not "teenagers" but final-year students at one university. Narrowing usually improves a study by making the population coherent.
- Same phenomenon, different vantage point. Can't observe the behaviour? Study the people who used to do it, the documents it generates, the professionals who respond to it, or the public debate about it.
- Same variables, existing data. Before collecting anything, ask whether someone with a research council grant already collected it. Secondary analysis of a major dataset is not a lesser dissertation - it's often a better one.
- Same design, shorter window. Two waves over eight weeks instead of four over a year. A pilot instead of a full study, honestly framed as such.
- Same ambition, one method. Cut the mixed-methods sprawl to the single approach best fitted to your question and do it to a standard that shows.
- Same causal interest, honest claim. Replace "prove X causes Y" with "examine the association between X and Y, and discuss what would be needed to establish causation." That sentence alone signals research maturity to an examiner.
Supervisors, incidentally, love this conversation. As we discussed in our article on what supervisors really mean, the questions they ask are the feedback - and "how would you do that?" is the most generous question of all, because it's asked before you've spent six months finding out the hard way. Arriving at a second meeting with "you asked how I'd get access - here are three options, and here's the one I think works" is exactly the move that turns a student into a researcher in their supervisor's eyes.
The bottom line
The gap between a brilliant idea and a workable research project is not intelligence or ambition; it's the discipline of asking six unglamorous questions before you start rather than discovering the answers when it's too late. Access, ethics, time, cost, data and fit will each be tested eventually - by an ethics committee, by an empty inbox, by a spreadsheet that never arrives, or by an examiner pointing out that ten people cannot prove anything. Far better that they're tested by you, on paper, in a proposal, while every one of them can still be fixed. The evidence says you'll be more optimistic than you should be about all six; plan for that. Then take your fascinating, impossible idea, move it one rung down the ladder, and build the version that will actually exist by the deadline. A finished study of a narrower question beats an unfinished study of a perfect one - every single time.
