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Strategy for NIH Funding
Navigation for the Strategy for NIH Funding. Link to Part 1. Qualify for NIH Funding.Link to Part 2. Pick and Design a Project.Link to Part 3. Write Your Application.Link to Part 4. Submit Your Application.Link to Part 5. Assignment and Review.Link to Part 6. If Not Funded.Link to Part 7. Funding.

Sidestep These Application Missteps

To err is human, to avoid errors divine, especially when you're applying for a grant. Mistakes can cost you a chance at getting funded, and when stakes are that high, you'll want to know how to steer clear of them.

Before you can swerve out of the way, however, you need to know what you're trying to avoid. To help you, we cover both bases—common pitfalls applicants run into and how to sidestep them.

To make this information as useful as possible, we're including advice from those in the know: program and scientific review officers (SROs) who have years of experience helping investigators try to get a grant. Based on what they've seen applicants do wrong, they share how you can do it right.

*We are in the process of updating our application missteps articles. We will repost them as they appear in upcoming issues of the NIAID Funding News.

Table of Contents

  • Weak Project
  • Misfiring on Innovation
  • Unfocused Hypothesis or Specific Aims
  • Flawed Project Design
  • Poor Writing and Presentation

Weak Project

First on our list of pitfalls to avoid: proposing a weak project, i.e., a project that reviewers will likely not score well for any one of the following flaws:

  • Lack of significance
  • Proposed project is a fishing expedition.
  • Problem more complex than investigator may realize

Lack of Significance

By having a project with little significance—one of the standard NIH initial peer review criteria—you likely seal your fate of not faring well in review. That's why it's absolutely critical to avoid this fatal flaw.

Ask yourself key questions

When thinking about the significance aspect of your application, you may find it helpful to answer for yourself the questions reviewers consider when they assess significance:

  • Does the project address an important problem or a critical barrier to progress in the field?
  • If the Specific Aims of the project are achieved, how will scientific knowledge, technical capability, and/or clinical practice be improved?
  • How will successfully completing the aims change the concepts, methods, technologies, treatments, services, or preventative interventions that drive this field?

Along this line of questioning, Frank DeSilva, scientific review officer (SRO), Scientific Review Program, also suggests:

"To help reviewers better understand the significance of an application, investigators should make an effort to address the following questions: Why is the work important? How will it push the field forward? What is the potential long-term effect that this research will have on science and public health? If an applicant does not clearly articulate these points, reviewers will likely lose enthusiasm for the application. Ultimately, the applicant must present a convincing case that the proposed research is a worthy investment of taxpayer dollars.”

Keeping all these points in mind, your job is to convey and convince in an objective manner. That is, clearly convey the significance of your proposed work so you can convince reviewers your project is worthy of funding.

"Having an ‘impact statement' gives the reviewers an opportunity to understand where things are going in the big picture. Applicants should provide a few sentences in their application that direct reviewers to that as well as future impact."—Michael Minnicozzi, program officer,  Division of Allergy, Immunology, and Transplantation (DAIT) 

To learn more, go to Highlight Significance and Innovation in the Strategy for NIH Funding, linked below.

Use sounding boards

Significance can sometimes be in the “eye of the beholder.” A good way to gauge whether your project is important is to seek advice from others you trust and see if they agree that your project’s objectives are significant.

A program officer in our Division of AIDS (DAIDS) suggests this:

"If you pitch your idea to people, do they get excited or do they comment 'so what?' If you can then convince them why your question is important, consider using that in your application. This means your project wasn't weak, just your justification. If they still aren't excited, consider another project."

SROs are also in favor of using a sounding board to determine whether you must go back to the drawing board:

"If applicants are unsure about the significance of their application, they should approach colleagues at their institution or trusted members in their field of study to help gauge the importance of the proposed research. We also encourage investigators to get advice from NIAID program officers. They know the field and the needs or gaps which are of interest to NIH. If you can't convince these people that your work is significant, it's time to go back to reassess your project."—Frank DeSilva

For requests for applications (RFAs), the narrow scientific scope and unique review criteria make your program officer's insight even more valuable.

"In the case of RFAs, your project needs to be significant in the context of the funding opportunity announcement. An investigator-initiated application may be highly significant when presented to a standing study section but not fully respond to the criteria described in an RFA."—Wolfgang Leitner, program officer, DAIT

Seek out what's high priority or a hot topic, but...

Savvy investigators will find out our high-priority areas by either speaking with a program officer or checking Concepts: Potential Opportunities, linked below. Though a smart move, don't make high priority the basis for describing the significance of your work. That also goes for "hot" topics.

"Investigators often anticipate that addressing a program's high-priority area will automatically establish high significance for their application. While it's important to recognize programmatic high-priorities, applicants must thoroughly convince the review committee of their project's significance, going well beyond a significance statement that simply hinges on what program is interested in."—Alec Ritchie, program officer, Division of Microbiology and Infectious Diseases (DMID)

"While some reviewers may rate the application's overall topic as highly significant (e.g., RSV vaccine development), the proposed methodology or approach may be seen as less significant (e.g., using a common adjuvant with a widely studied antigen). Thus, submitting an application on a hot topic or in a hot field does not necessarily ensure a high significance score. Our reviewers want to see science that will push the field forward, i.e., that the application will have a significant impact on science and/or public health."—Frank DeSilva

Little potential to produce information that can significantly advance the field

At the end of your project period, will you have solid outcomes or little or nothing to show for the time you invested in your work and the money NIH invested in you?

Reviewers will ask the same question. Here's how to help ensure they get the right answer.

"Little potential to produce information that can significantly advance the field is known as ‘incremental benefit to the field.' This is a difficult review hurdle to overcome...The applicant really needs to critically reassess the project's aims and hypothesis, and ask 'is it really cutting edge work?'"—Michael Minnicozzi

"While the question might be important (e.g., study of a new drug proposed to have lower toxicity/higher efficacy than standard of care), poor study design or feasibility issues could render the question unanswerable." —DAIDS program officer

"While a project may be addressing a high-priority area, be innovative, and have a solid approach, the applicant must also convince the review committee that the data or product will have a real impact on human health." —Alec Ritchie

Speaking of data, justify the significance of the data you'll likely generate by describing what you'll do with it (or what will be learned from it).

Remember, the key here is making a case to your reviewers that you'll not only produce data, but that you'll produce something that has an impact on the field or public health—now or in the future.

Proposed Project Is a Fishing Expedition

To avoid this misstep, show reviewers that you're focused, not floundering. Even an Exploratory/Developmental Research Grant (R21) needs direction.

Ensure that your project tackles an important and unique problem, that your hypothesis is well-focused and testable by your Specific Aims, and that your experiments can help meet these aims. If reviewers feel you're fishing for data and not pursuing a logical progression of experiments to answer specific questions, they will not be enthusiastic about your project.

Furthermore, make each aim an achievable objective, not a best effort, with clear endpoints your peer reviewers can easily assess.

Also, support your aims by having key preliminary data when you submit. This is critical—even if it means waiting for another receipt date to obtain the findings you need.

All of these points must come across clearly in your application, lest your reviewers get the wrong impression—and penalize you for it.

It could be in the aim(s)

If the people evaluating your application do get the impression that you've "gone fishing," it may have to do with your Specific Aims.

Frank DeSilva provides some insight:

"When reviewers comment on an application as a 'fishing expedition,' we tend to find that they are really commenting on the lack of focus in the Specific Aims. Applicants occasionally attempt to impress the review panel by proposing to do too much. The reviewers want two to four focused aims that directly relate to the overarching hypothesis or question posed."

Wolfgang Leitner echoes the sentiment about having too many aims:

"New investigators are frequently criticized for writing proposals that are overly ambitious by proposing too much work. Established investigators may have a history of accomplishing a lot of work in a short period of time, but new investigators have to establish a reputation first. They should therefore be realistic about what can be done in two to five years and propose the rest as future research."

And speaking of aims, you don't want to appear aimless, i.e., having no direction. Michael Minnicozzi addresses this point.

"Reviewers may believe that an investigator has no real understanding of the proposed work's direction. He or she should start with a specific hypothesis and have targeted aims to answer the question. The application should be like a story that describes the goal (question to answer) and how the applicant is going to meet it (the aims and approaches)."

Or it could be the type of project

You may also receive the "fishing expedition” remark in your summary statement based on the nature of your project, as two of our program officers point out.

"This comment is sometimes made when investigators propose secondary analyses of samples and data from large clinical studies. Ensure the samples and data being analyzed tie into an overall story so as not to appear as a fishing expedition. Also focus your questions. Otherwise, break up what you plan to do into more than one application." —DAIDS program officer

"We see this comment frequently with product development-related R01 projects. It's very important for an applicant to focus any exploratory aspect of his or her application and back it up with data as much as possible."—Alec Ritchie

Or it could be an impression you're giving

You may also get the "fishing expedition” response because you don't have enough preliminary data to establish what direction to go in.

"When PIs conduct surveys or gather data to develop a hypothesis, reviewers may view their projects as descriptive or as a fishing expedition. If possible, it's better to include preliminary data to point in a specific direction, rather than to have the reviewers trust that PIs will follow their leads appropriately.”—Annette Rothermel, program officer, DAIT

Problem More Complex Than Investigator May Realize

Another strike that could take you out of the running: underestimating how complex your project is.

Reviewers will be able to tell you've made this mistake by evaluating your budget, effort, Specific Aims, and time commitment:

  • Budget—asking for too little is a sign that you don't understand the scope.
  • Effort—setting an insufficient level of effort shows you're not aware of how much work is involved.
  • Specific Aims—not having the appropriate number of aims could mean you don't grasp the complexity of your proposed research.
  • Time—requesting too few years for your grant indicates you think your research may take less time than your scope requires.

Sometimes less is more, but in this case, not having or asking enough could be detrimental. To find out what you should consider when thinking about "BEST," see Your Project's Scope: Plot Your Boundaries linked below.

Here's another take from Michael Minnicozzi:

"Reviewers will often use the expression 'too mechanistic.' If this is true, then having strong statements on significance and future direction may appease them. Alternatively, they may feel that the PI has not truly addressed alternative directions or approaches. It may be that after generating a specific hypothesis, the PI has focused too narrowly with the aims and approaches."

Is it really too complex, or is it something else?

While your project may indeed be more involved or complex than you realize, determine whether that's actually the case; it may not be. Various factors could lead reviewers to assess that you're "in above your head."

Our DAIDS program officer has this for you to consider:

"Sometimes this comment is true, and sometimes it's poor grantsmanship. Did the reviewer say this because the investigator failed to state how labor-intensive or technically challenging an experiment is (so unable to judge whether the applicant is aware of the complexity)? Or did the reviewer conclude this due to unrealistic timelines or lack of investigator experience in the methods?"

And note what Alec Ritchie says:

"This could be a reality or could be the perspective of the reviewer(s). Applicants must thoroughly consider and present the scope, resources available, pitfalls, and alternative approaches. They should also vet their proposed project with all key persons and their peers. They could proactively state how thoroughly they have considered and addressed potential complexity and challenges—a critical concern to address upon revision."

A Last Word to the Wise

When you read your summary statement, you may see some of the points covered in this section. However, keep in mind this important caveat, borrowed from Know What a Summary Statement Means, linked below:

"...although your summary statement gives you critical feedback, it is not an exhaustive critique or a teaching tool containing every point reviewers found to be problematic."

Along these lines, here's a final piece of advice, courtesy of Michael Minnicozzi:

"Often reviewers will write these items in the summary statement but have ‘larger or other' issues during the meeting. All the more important that applicants read their summary statement, then talk with the program officer assigned to the application. He or she may have additional contextual insight that was not written in the summary statement."

Related Links

Last Updated August 19, 2015

Last Reviewed August 17, 2015