🎯 By the end of this lecture you will be able to…
- Explain what a research problem is and how it differs from a topic or a question.
- Justify why problem selection is the single most important decision in a research project.
- Identify the main sources from which good computing-science problems emerge.
- Apply the "funnel" technique to move from a vague interest to a concrete, researchable problem.
Imagine two students. Both are brilliant coders. One spends six months building a beautiful system that nobody needed and no examiner could evaluate. The other spends a week choosing a sharp, answerable question — and their project almost writes itself. The difference wasn't talent. It was the problem they chose.
1What exactly is a research problem?
A research problem is a clear, specific statement of an unresolved difficulty, gap, or question that is worth investigating and that research can actually address. It names a piece of the world we do not yet understand well enough — and commits you to reducing that ignorance.
Notice the three ingredients hiding in that definition:
- A gap — something unknown, unproven, unmeasured, or unsatisfactory.
- Significance — closing the gap matters to someone (science, industry, or society).
- Researchability — you can gather evidence to say something credible about it.
"Machine learning for healthcare" is a topic — a vast territory, not a problem.
"Deep-learning models for pneumonia detection lose accuracy when tested on X-rays from a hospital they were not trained on — but we don't know which preprocessing steps reduce this drop" is a research problem. It has a gap, it matters (patient safety), and you can test it.
Problem, question, and hypothesis — a family, not synonyms
These three are often confused. They are layers of increasing precision:
| Term | What it is | Computing example |
|---|---|---|
| Research problem | The broad unresolved difficulty | Federated learning is slow to converge on non-identically-distributed client data. |
| Research question | A focused, answerable question drawn from the problem | Does client-drift correction reduce communication rounds on non-IID data by ≥20%? |
| Hypothesis | A testable, falsifiable prediction | Adding a drift-correction term lowers rounds-to-target-accuracy versus FedAvg on CIFAR-10 non-IID splits. |
2Why the research problem matters so much
The problem is the keystone of your project. Remove it and the arch collapses. Here's the chain of consequences a good problem sets in motion:
- It defines your scope — telling you what to include and, just as importantly, what to ignore.
- It dictates your method — an empirical performance problem needs experiments; a "does this proof hold" problem needs mathematics.
- It sets your success criteria — you can only claim success against a clear problem.
- It determines significance — reviewers and examiners judge contribution relative to the problem's importance.
A friend says: "I'll just start coding a chatbot and figure out the research angle later." What are two concrete risks of choosing the solution before defining the problem? Jot down your answer before reading on.
Engineers are trained to build. So we often pick a technology ("I want to use transformers / blockchain / Rust") and then hunt for a problem to justify it. This is backwards. A technology is a tool; research is defined by the question it answers. Choose the problem first — then select the tool that fits it.
3Where do good problems come from? (Sources)
Good problems are not conjured from thin air — they are found, usually in one of these seven reservoirs. In computing science, the richest are the first three.
① Gaps in the existing literature
The most reliable source. Authors themselves hand you problems in the "Limitations" and "Future Work" sections of every paper. Read three recent survey papers in an area and the recurring "open challenges" almost are your candidate problems.
② New or evolving technology
Every new capability opens a frontier of unknowns. Large language models created fresh problems overnight: hallucination measurement, prompt-injection security, evaluation of open-ended output, inference cost. New hardware (GPUs, TPUs, edge devices) does the same.
③ Practical problems from industry & practice
Real systems break in instructive ways. Slow database queries, flaky CI pipelines, models that degrade in production, accessibility failures — practitioners' pain points are a goldmine of researchable problems with built-in significance.
- ④ Replication & contradiction: Two papers report opposite results — who's right, and under what conditions?
- ⑤ Theory: A model or theorem predicts something nobody has empirically checked.
- ⑥ Interdisciplinary transfer: A method from biology (genetic algorithms) or physics (simulated annealing) applied to a computing problem.
- ⑦ Personal observation & datasets: A pattern you noticed, or a newly released dataset that enables a question that was impossible before.
Every time you read a paper and think "but what about…?", or hit a bug that makes you wonder "why does this happen?", write it down immediately. Within a semester you'll have 30+ candidate problems. Researchers don't have one idea — they have a pipeline.
4Identifying a problem: the funnel technique
You cannot research "Artificial Intelligence." You can research something the size of a research question. The funnel narrows a broad interest into a workable problem through four steps:
| Step | Level | Example |
|---|---|---|
| 1 | Broad area | Computer vision |
| 2 | Topic | Medical image segmentation |
| 3 | Specific problem | Segmentation models need huge labelled datasets that hospitals rarely have |
| 4 | Research question | Can self-supervised pre-training match fully-supervised Dice score using only 10% of labels on breast-ultrasound scans? |
Vague interest: "I like cybersecurity."
Read + narrow: You read that phishing-detection models are often trained and tested on the same email dataset.
Spot the gap: Nobody reports how these detectors perform on phishing styles that emerged after training.
Frame the problem: "Phishing detectors may overstate real-world accuracy because they aren't evaluated on temporally-novel attacks."
Ask the question: "How much does detection F1 drop when a model trained on 2022 phishing emails is tested on 2024 emails, and does periodic retraining recover it?" — Now you have a project.
Pick any area you enjoy (games, networks, databases, mobile apps). Run it through all four funnel steps on paper. If step 4 fits in one sentence and you could imagine collecting evidence for it — you've just identified a research problem.
✅ Check your understanding
🧠 Key takeaways
- A research problem = a gap + significance + researchability. A topic is not a problem.
- Problem, question, and hypothesis are layers of precision, not synonyms.
- The problem is the keystone: it fixes your scope, method, and success criteria — so choose it first, before any technology.
- Good problems are found in literature gaps, new technology, and practical pain points — keep an idea log.
- Use the funnel (area → topic → problem → question) to reach something you can actually research.
Research Methodology in CS (CSEG3060) · Unit I · Lecture 1 · Dr. Mohsin Furkh Dar · UPES Dehradun