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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

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

Misfiring on Innovation

Next on our list of frequent stumbling blocks: innovation. Here we show you how to clear this hurdle.

As one of the standard NIH initial peer review criteria, innovation is used to assess how much a project can 1) shift the current research paradigm or 2) refine, improve, or propose a new application of an existing concept, method, instrumentation, or clinical intervention.

In deciding which part of the definition to satisfy, take note that you don't need to make one giant leap for science.

Illustration: starburst graphic showing how your research pushes the borders of your scientific field outward.Taking incremental steps is fine as long as you clearly show how your project will move the ball down the field, adding significantly to knowledge and pushing its frontier forward, as illustrated by the graphic on the right.

In short, you should be on the cutting edge without going over the edge.

With this in mind, be aware that paradigm-shifting research can be an uphill climb, especially for new investigators or people entering a new field. You'll have to convince reviewers that it's feasible and that your preliminary data are strongly supportive of a possible paradigm shift, while being aware that some reviewers might think that challenging the status quo means challenging their world view or research.

Depending on your circumstances, a better plan may be to take the second approach. Most investigators, whether new or experienced, choose this route by showing how their proposed research is new and unique, e.g., explores new scientific avenues, has a novel hypothesis, or will create new knowledge.

Along those lines, a program officer in our Division of AIDS (DAIDS) expands on how applicants can demonstrate innovation: "Innovation can take many forms. It can include using a new technology. It might involve developing new animal models or combining disciplines to tackle a problem."

To learn more, go to Be Innovative, But Be Wary in Part 2 and Innovation in Part 3 of the Strategy for NIH Funding, linked below.

Reviewers and Innovation

Of course, how you fare with innovation depends on your reviewers, who will likely fall into two categories: those who readily grasp and appreciate the cutting edge elements of your project (and will thus give you a good innovation score), and those who may not be as receptive to these same elements (and will thereby give you a poorer score).

Make Sure Each Reviewer "Gets It"

To help get as many people on your side as possible, it's essential to clearly convey what is innovative about your proposed work so that all your reviewers—experts and non-experts alike—"get it."

Our DAIDS program officer seconds this notion:

"Applicants must set the stage so that all reviewers, no matter what their background, can appreciate the project's innovative aspects. For example, if an investigator proposes applying tried-and-true 'Technology X' to develop a rapid diagnostic test for an organism that clinicians have a dire need to identify, he or she should address 1) reviewers who are familiar with the technology but not with the organism and thus may not see the innovation in using a well-established technology to address this diagnostic need and 2) reviewers who understand the organism and why a rapid diagnostic test is necessary but who are not familiar with the technology and the feasibility of its use for the new test."

For more on addressing your reviewers, go to Know Your Audience, linked below.

Address How Your Project Does and Doesn't Fit the Innovation Shoe

Highlighting your project's innovative aspects is important but so is pointing out where innovation is not essential. Two of our program officers explain why covering both bases is crucial.

"Many reviewers interpret this criterion as a requirement to develop or use novel technologies or techniques, so they often criticize or penalize applicants who use 'standard and established techniques' even if they're the most appropriate. Given this, applicants should explicitly describe at what level their project is innovative, i.e., at a technological or scientific level (innovative hypothesis or model system), or both! If they're not developing new technologies, techniques, or protocols, they shouldn't hesitate to point that out themselves and explain why."—Wolfgang Leitner, program officer, Division of Allergy, Immunology, and Transplantation (DAIT)

"Since innovation is a standard review criterion, reviewers have to evaluate this factor, even for later stage product development applications that are frequently devoid of innovative approaches. I encourage applicants with projects that rely on straightforward methodologies to highlight any other novel aspect of the project, such as how the technology or product will be applied or integrated in a new way. In the absence of any identifiable innovation, applicants should acknowledge or briefly explain why their project lacks the innovation reviewers are charged with looking for."—Alec Ritchie, program officer, Division of Microbiology and Infectious Diseases (DMID)

Persuade Reviewers of Your "Risk"y Business

Introducing anything new or unique has its risks. Think of gadgets, like smart phones and e-readers, that have come out over the last few years. The creators had to convince people, whether business partners or shareholders, that their innovative product was worth the risk and destined for success.

Here are some tips on how to do that.

Frank De Silva, a scientific review officer in our Scientific Review Program, advises:

"Depending on the proposed research, reviewers may view innovative ideas and technologies as risky. Consequently, applicants should thoroughly describe why the innovation being described (be it an idea or technology) is important in moving the scientific field of interest forward. For innovative ideas, it should be rational and supported by the literature and, if possible, preliminary data. With innovative technologies, the application should indicate experience with the proposed methodology, provide some preliminary evidence that it is feasible and appropriate, and consider possible alternative approaches to address potential problems and limitations, i.e., mitigate the potential risk."

Our DAIDS program officer adds:

"Innovation often involves an element of risk. That said, the more you can demonstrate the feasibility of your project, the better. For example, has the proposed technology been used before? Do you or your team members have experience with the technology? If you've used it but not for this organism, have you demonstrated that you appreciate the challenges that a different organism poses? If you propose something that is really outside the box, consider an initiative, e.g., a request for applications, that is seeking this."

As an example, see Innovative Technologies and Assays in Support of HIV Cure Research (ITAS-Cure) (R41, R42) and (R43, R44) on our NIAID Funding Opportunities List. Read more about applying for initiatives that call for innovation in Getting a Grant for Innovative Research. For a list of other innovation-seeking initiatives, go to The NIH Common Fund's High-Risk Research page. Both resources are linked below.

Give Yourself Time, Ask Yourself Questions

Now that you know some of what to expect when it comes to reviewers, you probably see that it's wise to give the innovation aspect of your application time and consideration. Don't leave it as an afterthought; you should be thinking about innovation early on, as one of our program officers advises:

"The innovation criterion should be in mind as applicants develop their research question and Research Plan. They certainly shouldn't wait until they get to the Innovation section of the Research Strategy to start thinking about how to address the innovative aspect of their research."—Annette Rothermel, program officer, DAIT

As you ponder innovation from the get-go, you might find it useful to ask yourself some key questions to gauge whether reviewers will think your project fits the bill.

Wolfgang Leitner suggests these:

"I would recommend that applicants ask the following: Is my approach unique and my experimental design creative, unconventional, or multidisciplinary? Will I generate novel, meaningful insights? Answering 'yes' will likely garner high marks for innovation.

However, a low innovation score is guaranteed if applicants play it very 'safe,' e.g., their scientific approach is very conservative, the scope of the research is narrow, and the proposed study is more of the 'same old, same old.'

Playing it safe also includes the uncritical embrace of dogmas and established models in the field instead of following up on findings that are or appear to be inconsistent with the models and do not support the commonly held beliefs.

While it is not necessary to propose a radical overturn of imperfect models, refining and correcting them will benefit the research community, thus move the field forward and likely be rewarded with a good innovation score."

Related Links

Unfocused Hypothesis or Specific Aims

After covering must-avoids like proposing a Weak Project and Misfiring on Innovation, we now tackle another pitfall to sidestep: lack of focus in your hypothesis and Specific Aims.

In this context, we use the term "unfocused" rather than "weak" since the two are different.

"Weak" relates to a project's impact and significance. Though an application may be weak, it can still be focused.

"Unfocused" relates to the lack of a strong central hypothesis, which can be too broad (e.g., inflammation is a key etiological component of autoimmune diseases) or too descriptive (e.g., we will evaluate changes in transcriptional signatures in the involved tissues following infection).

Why Focus Is Key

To paraphrase a popular saying, your application is only as strong as its weakest link—and you certainly don't want that link to be either your central hypothesis or your Specific Aims. One of our program officers explains why:

"An application with an unfocused central hypothesis or Specific Aims that won't rigorously test the underlying concepts will most likely not be discussed at review. These constitute the foundation of a project, so a lack of focus will strongly reduce reviewer enthusiasm for the project."—Alec Ritchie, Division of Microbiology and Infectious Diseases (DMID)

Hypothetically Speaking

Coming up with a solid central hypothesis for your application may be more challenging than you might think.

Not only should it be well-focused and testable (through your Specific Aims), but it has to be sound and important enough that reviewers believe your research will be able to make a high impact on its field.

With so much riding on your central hypothesis, it's crucial you think carefully about it, considering whether it forms a solid foundation for your Specific Aims.

To gauge the quality of your hypothesis, a program officer in our Division of AIDS (DAIDS) gives you a starting point:

"Ask yourself: Did I begin with a hypothesis then develop the aims and approach to address it? Or did I build the hypothesis around existing data and samples so it would fit what was available to me? The latter approach sometimes results in an unfocused hypothesis or the appearance of a 'data gathering' exercise."

What Makes a Good Hypothesis

From the perspective of reviewers as well as our program and scientific review staff, the saying "you'll know it when you see it" could apply to a focused (strong) hypothesis. In other words, there are not discrete definitions for focused and unfocused hypotheses. That said, our experts describe what does and does not make a good hypothesis.

DMID's Alec Ritchie offers this:

"Alone or together, these major factors contribute to an unfocused hypothesis: 1) insufficient or poorly interpreted preliminary data that the hypothesis is built upon and 2) unlikelihood of fully and objectively testing the hypothesis."

Another program officer, Wolfgang Leitner of our Division of Allergy, Immunology, and Transplantation (DAIT), echoes the sentiment about preliminary data as he describes two categories of suboptimal hypotheses:

"Those that are either based on weak preliminary data or not supported by the preliminary data (i.e., they may be very specific and focused but have no factual basis).

Then there are those that make the reader ask, ‘So what?' A hypothesis may not be considered strong because the research community doesn't think the question is interesting. It may have been answered already or it doesn't add anything to our understanding of the system. Therefore, confirming the hypothesis would have no significant impact on the field."

Jim Turpin, a program officer and branch chief in DAIDS, provides a lengthier description:

"A good central hypothesis is a balance of two components: an addressable scientific gap and the knowledge base needed to support the hypothesis. The knowledge base may come from supporting scientific literature or the investigator's experience and publication record.

Reviewers often judge the strength of a hypothesis by how these two factors synergize to create a compelling rationale for the proposed research. This synergy is often characterized as focus, which is important for how a reviewer perceives the hypothesis and its supporting Specific Aims."

For examples of effective and poorly focused hypotheses, go to Choose a Testable Hypothesis in our Strategy for NIH Funding, linked below.

Presenting Your Hypothesis

Once you've settled on a central hypothesis, you'll want to keep it fresh in reviewers' minds by mentioning it in various parts of your application. According to our experts, your hypothesis should feature prominently in at least two places: the abstract and Specific Aims.Wolfgang Leitner explains:

"The proposed project makes its first impression through the abstract and the Specific Aims sections, which consequently have a significant impact on how reviewers will score the entire application. Therefore, it is crucial for the central hypothesis, which the project is based on, to have a prominent position in these sections rather than to be introduced in the main body of the application."

Our DAIDS program officer suggests stating the hypothesis in the abstract and using a diagram in the Research Strategy to focus an application:

"Indicate what your hypothesis is early in the abstract so you don't lose reviewer interest. To help focus a pathogenesis or mechanistic application, consider including in the Research Strategy a diagram of the pathways hypothesized and tested. This diagram could help 1) the reader understand what is currently known and the gaps in knowledge that your project will address and 2) you better understand the analyses needed to test each hypothesis."

Frank DeSilva, a scientific review officer in our Scientific Review Program, addresses investigators responding to requests for applications (RFAs):

"It is important that the hypothesis is in line with the objective of the RFA and should be stated in the Specific Aims, which is one of the most important parts of an application since it serves as the first impression of an investigator's proposed research."

Getting Specific About Specific Aims

Your Specific Aims are the objectives for your research. To keep yourself from going off in too many directions, determine what two to four aims you could achieve within the proposed project period.

Focus your aims by making each one an achievable objective with clear endpoints your peer reviewers can easily assess.

Also maintain focus by never losing sight of your hypothesis, which goes hand in hand with the objectives of your project. In fact, the link between the hypothesis and aims is crucial, as two of our program officers point out:

"It's critical that the Specific Aims be designed to test the hypothesis as productively and directly as possible within the budget and timeline proposed, while allowing for pitfalls and alternative approaches to be negotiated as need be."—Alec Ritchie

"It must be clear to reviewers that the proposed aims are based on, and closely linked to, the central hypothesis. I would recommend paying close attention to the wording of the Specific Aims. Avoid (as much as possible) terms such as characterize, analyze, evaluate, or screen. They indicate a descriptive study that may not be asking mechanistic questions designed to address the central hypothesis."—Wolfgang Leitner

Focusing the Specific Aims Section

As part of your application's Research Plan, your Specific Aims section carries a lot of weight, despite its being limited to just one page (for R01s).

In it, you'll tell reviewers everything they need to know about the central hypothesis, research objectives, and significance of the proposed studies. Since all your reviewers read this part of your application, it's important to pack a punch by getting them excited about your project.

With little room to convey your aims, you'll want to keep them as focused as possible and cover the following bases:

  • Narrative that includes the "big picture" goal of your project and how the aims address an important scientific question or fill an important gap in understanding the big picture.
  • Statement of the central hypothesis and general approach you'll use to test it.
  • Brief description of your aims and how they build on your preliminary studies and previous research.

When responding to an RFA, the Specific Aims must address both what you propose to do and what the RFA is seeking, in terms of research objectives. Frank DeSilva provides some pointers for investigators applying to an RFA:

"The Specific Aims page should briefly describe the question(s) that you are trying to answer in response to the scientific objectives in the RFA, the stated hypothesis to address the question(s), a very brief background, and the significance of the work. Conclude with an impact statement stating how the results, if successful, will advance the scientific field of interest."

For advice on writing the Specific Aims section of your application, go to Explain Your Aims, and to see examples of focused Specific Aims, go to Sample Applications and Summary Statements. Both resources are linked below.

Related Links

Last Updated October 22, 2015

Last Reviewed October 22, 2015