finance-idea-screening

Finance Idea Screening

Turn rough topics into credible paper ideas or kill weak ideas early.

Stage 0: Desk-editor screen

Before running the full literature search and scoring workflow, answer four questions in 1-2 sentences each:

1. Prior-changing: What broad finance prior would change if this paper is right?
2. Zero-result value: Why would the paper still matter if the main estimate is zero or the sign flips?
3. Question over method: Is the question more important than the shock, instrument, or dataset?
4. Desk read: Could this clear a top generalist journal's desk read today?

If two or more answers are weak, return Revise or Kill before investing in the full search chain.

Framing rule: If the one-sentence summary starts with "Using a novel dataset..." or "Exploiting a policy shock...", force a rewrite until it starts with the finance question. The question must come first; the data or design is the tool, not the contribution.

What counts as a strong idea

A strong idea scores well on six dimensions:

1. Sharp question — Can you state the research question in one sentence without hedging? Is there a clear dependent variable and a testable prediction?
2. First-order importance — Would the answer change priors in a broad finance literature or on a materially important market, policy, or contracting problem? Would a generalist finance editor care even if the estimated effect is zero?
3. Verified contribution — Relative to the 3-5 closest papers, is the novelty real and nontrivial? Novelty must be in mechanism, question, identification, measurement, or implication, not just in setting, time period, or data access. "X but in country Y" or "X but with newer data" is not a contribution unless the setting variation generates a genuinely different economic prediction.
4. Economic mechanism — Is there a friction, incentive, or equilibrium force that generates a testable prediction? Can you name the channel and distinguish it from obvious alternatives?
5. Convincing theory-to-evidence bridge — Is there a persuasive inferential bridge from idea to evidence? This can be a quasi-experiment, field experiment, theory model, structural estimation, validated measurement exercise, sufficient-statistic approach, or out-of-sample asset-pricing test. Judge whether the bridge matches the question, not whether it looks like a standard causal design.
6. Data, measurement, and replication feasibility — Three sub-checks:
7. Access: Can the data realistically be obtained in time?
8. Construct validity: Does the empirical measure actually map to the mechanism? Would a skeptic accept it as a reasonable proxy?
9. Replication feasibility: Could the core result be documented and replicated under current top-journal data and code sharing policies?

Scoring rubric

Rate each of the six dimensions 1-5:

• 5: Publication-grade strength — among the best you could imagine for this dimension
• 4: Strong — needs only minor refinement, no fundamental concern
• 3: Promising — needs significant work but a clear path exists
• 2: Weak — major gap that may or may not be fixable
• 1: Fatal — unlikely to be resolved

Calibration guidance:

• Default to 2 or 3 unless there is a strong, specific case for higher.
• Use 5 sparingly. A 5 means this dimension would survive the toughest referee in the field.
• Never rate an idea as top-3 Go if the only clear strength is data access or a clever shock.
• A paper that is 3 across the board is a plausible working paper or field-journal candidate, not a top generalist journal paper.

Decision rules:

Top Generalist Go

• Importance >= 4
• Contribution >= 4
• Bridge >= 4
• No dimension < 3
• At most 3 essential hurdles to publication

Strong Field-Journal Go

• All dimensions >= 3
• Total >= 18
• One or more of importance, contribution, or bridge is 3 rather than 4, but the overall package is solid

Revise

• The question may matter, but at least one of contribution, bridge, or construct validity is underdeveloped
• Total 15-20 with a clear path to improvement on the weak dimensions

Kill / Pivot

• Importance < 3 (the question is second-order)
• Contribution is mostly setting variation
• The bridge cannot distinguish the proposed mechanism from obvious alternatives
• More than 3 essential hurdles would be needed for publication
• Total <= 14 or any dimension = 1

Revision-feasibility rule

After scoring, list the essential hurdles a referee would raise. Apply this filter:

• If more than three essential hurdles are needed to make the paper publishable, default to Kill or Pivot unless the question is unusually important (Importance = 5) and the contribution is unusually novel (Contribution >= 4).
• Ask whether a plausible path to publication exists within one R&R round, or at most two. If not, the idea is not ready.

Imaginary abstract test

Before running the full scoring workflow, write a 5-part imaginary abstract for the idea:

1. Motivation/Tension: What is the gap between what economists assume and what the world actually looks like? What prior would change?
2. Empirical Setting and Data: What is the ideal experiment or setting? What data would you use?
3. Results: What would you expect to find? Be specific about magnitudes if possible.
4. Implications: What does this mean for theory, practice, or policy?
5. Conclusion: One-sentence takeaway.

Purpose: The imaginary abstract forces coherence. If you cannot write a plausible 5-part abstract, the idea is not ready. Ideas that sound exciting as a sentence but collapse when spelled out are Type I errors waiting to happen. The goal is not to draft a flawless abstract, but to test whether the idea has substance.

If the abstract feels impossible to write, that is diagnostic: the idea lacks a clear question, a plausible test, or a meaningful result. Kill or revise.

Four quick stress tests

Apply these after scoring. Each should be answerable in one sentence.

1. Null-result value test: State what the paper teaches if the main estimate is zero. If the answer is "nothing," the paper is too dependent on a specific result.
2. Simultaneous-discovery test: If a similar working paper appeared on SSRN tomorrow, would this paper still deserve publication because it gives the cleanest, most credible, or most important answer? If not, speed-to-market is the only edge, which is fragile.
3. Syllabus test: Name one sentence in a PhD finance lecture that would have to change if the paper is right. If you cannot, the paper may not be first-order.
4. Necessary-conditions test: Name the one critical first-stage condition that must hold for the project to work (e.g., the shock must show up in the data, the treatment must change behavior, the instrument must have a first stage). Can you check this condition with a few hours of work before committing months? If the necessary condition fails, kill the project early. Treat research like drug development: lab test before clinical trial.

Kill criteria

Flag the idea as weak if one or more of these dominate:

• It is a minor setting variation with no new mechanism ("X but in country Y").
• The identification is decorative rather than essential — the result does not require the proposed design.
• The data are unavailable, too small, or too noisy for the claim.
• The contribution depends on saying "first" without verification.
• The likely result would be too local or too descriptive for the intended journal.
• The idea needs multiple heroic assumptions to work.
• The question has been answered convincingly and the proposed paper cannot improve on existing answers.
• The mechanism is a just-so story with no way to distinguish it from alternatives.

Screening workflow

1. Stage 0: Run the desk-editor screen (four questions above). If weak, stop early.
2. Restate the idea in one sentence (question-first fra