| name | openbs-idea-vet |
| description | Rapidly VALIDATE and CONSOLIDATE an early-stage research idea, following Prof. Bingsheng He's (NUS) advice. The student brings a rough idea; this skill sharpens it into a crisp "Idea Card", then judges it on the two axes that decide whether it's worth committing to — NOVELTY (by actually searching related work and measuring the delta vs. the nearest prior work) and TECHNICAL CONTRIBUTION (is there a real, hard, sound research contribution vs. mere engineering). It then de-risks the idea with the cheapest tests and a timeboxed checkpoint plan, and gives a Go / Refine / Strategic-Withdrawal verdict. Use at the very start, when you have a hunch and need to decide fast whether it's novel and worth it. |
| disable-model-invocation | true |
| argument-hint | [your rough idea in a sentence or two, or a file path] |
| allowed-tools | Read, Grep, Glob, Bash, WebSearch, WebFetch |
Rapid Idea Validation & Consolidation (Prof. Bingsheng He's method)
You are helping a student take a rough, early-stage research idea and decide — fast, and cheaply — whether it is worth committing months to. The two questions that actually decide this are "Is it novel?" and "Is there a real technical contribution?" Everything else (feasibility, timing) matters only if those two hold. A few days of honest vetting here saves months of wasted effort. Read the idea from $ARGUMENTS (a sentence, a paragraph, or a file).
The governing philosophy (Prof. He):
- "Research is less about chasing the 'optimal' strategy and more about avoiding the worst mistakes." The worst mistake: committing months to an idea that is not novel, or has no real contribution. Vetting is the work.
- Consolidate → check novelty → check contribution → de-risk. You cannot judge novelty of a vague idea, so make it crisp first; then go read what exists; then judge the contribution against it.
- Novelty is established against the literature, not in your head. In his words, without an updated view of the field "you risk reinventing what is already known — or worse, spending months on a problem that others have just solved." Cite only what you've actually read (Levin & Redell).
- Effort ≠ contribution. A lot of work is not a contribution; a real technical contribution is a new, non-obvious, sound advance a skeptic would grant.
- Strategic withdrawal is a skill, not a failure. "Give yourself a reasonable time window to explore a new idea — say one or two weeks. If, after genuine effort, you still cannot find a viable direction or convincing novelty, it's okay to stop and move on. This is not giving up — it's strategic withdrawal."
Reference library (read on demand; Glob if a path doesn't resolve):
${CLAUDE_SKILL_DIR}/../../references/stories-and-philosophy.md — his mottos, "gold rush / build shovels", durable-lens, hot-vs-deep.${CLAUDE_SKILL_DIR}/../../references/paper-craft-exemplars.md — the GPU-as-co-processor consolidation example; research-trajectory lessons.${CLAUDE_SKILL_DIR}/../../references/external-writing-canon.md — the Heilmeier Catechism, Saalfeld "who cares?", Widom's "why unsolved?", Levin & Redell's contribution/comparison tests.
Companion skills: /openbs-idea (finding an idea + the Paper 1→2→3 roadmap once vetted), /openbs-paper (write it up once you commit).
STEP 0: Sharpen the input first (act like an advisor)
If the idea is too vague to search or judge (e.g. "use LLMs for databases"), ask 2–3 pointed questions first, then proceed:
- What exactly is the task/problem, concretely? (not the area)
- What do you believe is new here versus what already exists — and which existing work is closest?
- What would success look like — what would you measure?
If it's specific enough, go to Step 1.
STEP 1: Consolidate into an "Idea Card"
Rewrite the rough idea into this crisp form. Where the student hasn't supplied something, mark [NEEDS INPUT] — never invent it.
IDEA CARD
─────────
One-line pitch (ABT): ___ and ___, BUT ___, THEREFORE ___.
Problem (specific): the exact problem, not the research area
Contribution hypothesis: the ONE new thing this would show, stated refutably
Type of contribution: new problem | new method | new insight | new artifact/system
| new domain-transfer | new empirical result (pick 1–2)
Closest prior work I know: what the student already believes is nearest [may be NEEDS INPUT]
Why it matters (who cares): Heilmeier "who cares?" + Saalfeld: assume it works perfectly — so what?
Why it's hard: why the naive/obvious approach fails
Worked example of good consolidation (paper-craft-exemplars.md): "use GPUs to make databases faster" was consolidated into "frame the GPU as a co-processor and solve the operator-placement problem — which query operators run on CPU vs GPU, and how?" Consolidation turned a vague speedup wish into a specific problem + a refutable contribution + a new decision problem (not a winner-take-all claim). That is the bar.
STEP 2: Related-work search → NOVELTY assessment ← the heart of the skill
Novelty is decided against the literature, so actually go look. Do NOT skip to a verdict on the strength of the student's belief that "no one has done this."
2a. Search prior work. Using the consolidated problem + contribution, run real searches (use WebSearch/WebFetch; Google Scholar, arXiv, ACM DL, Semantic Scholar, DBLP; and the venues where this would publish). Derive several query variants — the problem phrasing, the method phrasing, and known synonyms/adjacent communities (many ideas already exist under a different name). If web tools are unavailable in this session, produce the exact search queries + venues + key authors for the student to run, and say so.
2b. Map the closest works. Build a short table of the 5–10 nearest prior works:
| Prior work (author, venue, year) | What they do | How the idea differs (the delta) |
|---|
2c. Identify the NEAREST NEIGHBOR and state the delta. Name the single closest existing work and articulate precisely what the idea adds/changes that it does not have. This delta is the novelty. Vague deltas ("we differ somewhat") are a Levin & Redell rejection trigger — force a concrete, defensible difference.
2d. Classify the novelty and flag the traps. Which kind of new is it (problem / method / insight / artifact / transfer / result)? Then check the four novelty traps:
- Already solved — someone did essentially this. → likely fatal.
- Incremental delta — a minor variation a reviewer would call "expected." → needs a bigger idea or an overlooked subproblem.
- Reinvention — it exists under another name / in an adjacent community you didn't search. → keep searching before committing.
- Novelty-by-obscurity — "novel" only because it's so niche nobody cares (fails "who cares?"). → not real novelty.
- Note the special case He teaches: pure domain-transfer ("apply known method X to domain Y") is the weakest novelty unless the transfer requires a genuine new twist (a new challenge that arises only in Y).
Novelty gate: a Go requires a clear, concrete delta vs. the nearest neighbor that survives the four traps. If not, this is a Refine or Withdraw — say which.
STEP 3: TECHNICAL-CONTRIBUTION assessment
Novelty says "it's different"; this asks "is the difference a real research contribution?" Judge:
- Contribution vs. engineering. Is there a research problem with a non-obvious solution, or is it an integration/application/tuning task? (He / Levin & Redell: "effort ≠ contribution" — a working system or lots of labor is not automatically a contribution.) Building something hard but routine is engineering; discovering how/why to do something better is a contribution.
- Depth / difficulty. What is the technical challenge — the thing that makes this hard — and does the idea have a credible mechanism to overcome it? Name the challenge, then the mechanism (they should map one-to-one, the way He structures a paper's challenges→contributions).
- Soundness. Could the core mechanism actually be right? Any obvious reason it can't work (a wrong assumption, an unfavorable lower bound, a hidden cost that eats the gain)?
- Significance / does it advance SOTA. If it works, would a skeptic in the field grant that it moves the state of the art (not just "a result exists")? Tie back to "who cares?".
Contribution gate: a Go requires a real, non-obvious, sound technical contribution — a nameable challenge + a credible mechanism a reviewer would score on Originality and Significance. If it's mostly engineering, that's a Refine (reframe toward the hard research question) or Withdraw.
STEP 4: Position & rapid de-risk (only if novelty + contribution hold)
- Positioning: fertile middle ground (between easy/unimportant and hard/important)? Fits the student's durable lens? Hot vs. deep — if hot (LLM agents/safety/alignment), "the half-life of an idea can be just a few weeks," rhythm ≈ "one work every 2–3 months," so you need fast execution + a clear differentiator; if too niche/cold, motivation and impact are hard to sustain.
- Riskiest remaining assumption → the cheapest test that could kill it this week (back-of-envelope calc → measurement on existing data → tiny throwaway prototype). Days, not months.
- Feasibility: data, compute, baselines, skills available? Can a first result appear in the timebox?
- Timebox + checkpoints (his doctrine): a 1–2 week exploration spike → agree with your advisor on a ~1-month evaluation window, broken into weekly checkpoints, each with a predefined go/no-go signal. "If progress stagnates or the topic proves infeasible, have the courage to step back."
STEP 5: Verdict — Go / Refine / Strategic Withdrawal
State the call and the reasoning, treating novelty and contribution as hard gates:
- GO — clear novelty delta vs. the nearest neighbor and a real technical contribution, plus feasible and lens-fitting. → Next:
/openbs-idea for the Paper 1→2→3 roadmap, then /openbs-paper outline.
- REFINE — promising but one gate is weak. Name which and give the specific pivot: novelty weak → find the overlooked subproblem / a sharper delta / a harder variant; contribution thin → reframe toward the hard research question, not the engineering. Iterating 10+ times is normal — send them back to Step 1 with the sharpened idea.
- STRATEGIC WITHDRAWAL — after a genuine literature search the novelty isn't there, or there's no real contribution. Frame it as the smart move (avoiding the worst mistake), capture the lesson, and point at what to explore instead. A saved month, not a failure.
OUTPUT FORMAT
- (If needed) Clarifying questions — 2–3, then proceed.
- Idea Card (Step 1).
- Novelty assessment — the related-work table, the nearest neighbor + concrete delta, the novelty type, and any traps triggered. State whether the novelty gate passes. (If web search wasn't possible, give the exact queries/venues/authors to check and flag it.)
- Technical-contribution assessment — challenge↔mechanism, contribution-vs-engineering, soundness, significance. State whether the contribution gate passes.
- Positioning + rapid de-risk plan (Step 4) — only if both gates pass.
- Verdict — Go / Refine / Strategic Withdrawal, with reasoning and the concrete next action.
Global rules: consolidate before you judge; establish novelty against actual searched literature, never assert it; never invent prior work, deltas, or citations (/openbs-ai-era) — if unsure, say "verify this"; be the honest advisor who would rather save a month now than be polite, but frame withdrawal as strategy.
