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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.

Note: SRO Brandt Burgess (quoted below) is no longer at NIAID.

Table of Contents

Weak Project

First on our list of traps to dodge: proposing a weak project, which comprises these areas:

  • Lack of significance.
  • Little potential to produce information that can significantly advance the field.
  • Proposed project is a fishing expedition.
  • Problem more complex than investigator may realize.

Lack of Significance Is Significant

By having a project without significance—one of the standard NIH initial peer review criteria—you likely seal your fate, i.e., not faring well in review and therefore losing out on a chance at funding. That's why it's absolutely critical to avoid this fatal flaw.

Here's advice on how.

Use sounding boards

A good way to gauge whether your project is important is to bounce it off of other people and see what sticks.

Susan Brobst, 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."

Scientific review officers (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 the drawing board."—Brandt Burgess and Frank DeSilva, Scientific Review Program

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 our Council-approved concepts. 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."—Brandt Burgess and Frank DeSilva

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 aims of the project are achieved, how will scientific knowledge, technical capability, and/or clinical practice be improved?
  • How will successful completion of the aims change the concepts, methods, technologies, treatments, services, or preventative interventions that drive this field?

Along this line of questioning, our SROs also suggest:

"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.

Potentially Problematic: 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.

"[The concept of producing] is also 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." —Susan Brobst

"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.

Gone Fishing: Proposed Project Is a Fishing Expedition

To avoid this misstep, show reviewers that you're focused, not floundering.

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.

Brandt Burgess and Frank DeSilva provide 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, another program officer in DAIT, 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." —Susan Brobst

"We see this comment not infrequently with product development-related R01 projects. It's very important for an applicant to focus any exploratory aspect of their application and back it up with data as much as possible."—Alec Ritchie

It's Complex: 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 "BEST":

  • 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."

Susan Brobst 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 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.

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, Susan Brobst, 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."

Susan Brobst 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 too 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.

And that's the boat you're in with your research. To score well on innovation, you'll have to engage your power of persuasion to get your reviewers on board.

Here are some tips on how to do that.

Brandt Burgess and Frank DeSilva, scientific review officers (SROs) in our Scientific Review Program, advise:

"Reviewers often view using innovative ideas and technologies as risky. Consequently, applicants should thoroughly describe why the innovation being described (be it an idea or technology) is important to moving the scientific field of interest forward. For innovative ideas, it should be rational and be supported by the literature and if possible, preliminary data. With innovative experimental assays or technologies, the applicant should adequately address possible alternative plans if proposed experiments do not work, i.e., mitigate the potential risk."

Susan Brobst 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., an RFA, that is seeking this."

Read more about applying for initiatives that call for innovation in Getting a Grant for Innovative Research. For a list of 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 observe changes in transcriptional signatures in the involved tissues following infection).

Specific Aims can be unfocused if they lack specific goals and either overly describe or inadequately describe what the aim intends to accomplish.

Why Focus Is Key

To paraphrase a popular saying, your application is only as strong at its weakest link—and you certainly don't want that link to be either your 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 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 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, Susan Brobst, 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's no easy way to explain what makes a hypothesis focused or not. That said, our experts provide some insight.

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 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."

Susan Brobst 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."

Brandt Burgess and Frank DeSilva, scientific review officers in our Scientific Review Program, address 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.

Brandt Burgess and Frank DeSilva provide 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

Flawed Project Design

When flawed, project design can spell trouble for your application, so it's important to think about it carefully during the planning stages. Here's some advice to help you avoid this potentially damaging misstep.

Note: We cover a few basics of project design in this section. To learn more, see Design a Project in our Strategy for NIH Funding, linked below.

Build Your Foundation: Hypothesis and Specific Aims

As the driving forces for your project, the central hypothesis and Specific Aims are essential to its design. For more information on both elements, go to the resources in Related Links below. Our participating program officers touch on a few additional points here.

A central hypothesis is crucial since reviewers will examine it closely, but it can be difficult to develop, especially if you're proposing a brand new project or one that changes direction.

In those cases, you may have to include a fair amount of descriptive preliminary data to define basic parameters. Unfortunately, descriptive data often does not excite reviewers. Keep this in mind as you design your project and write your application.

Wolfgang Leitner, a program officer in our Division of Allergy, Immunology, and Transplantation (DAIT), has these tips for you:

"Make sure to a) keep the descriptive ('model-development/characterization') aspects of the project to a minimum and b) justify them well (ask yourself: do I really need to conduct a comprehensive characterization in order to proceed with the mechanistic aims or would a more targeted and selective characterization provide enough information?)."

In designing your project, be mindful to develop Specific Aims that are based on, and test, your hypothesis. Also establish a close link between the two. You'll need to demonstrate this connection clearly to your reviewers, as another DAIT program officer points out:

"Reviewers like to see a central hypothesis and how the Specific Aims address it. It can be helpful to fully lay out the hypothesis in the aims section, then conclude with a clear summary of what the applicant expects to know at the end of the award, how that fits with the hypothesis and thus drives the field forward, and where the project could go in the future."—Annette Rothermel

As for the Specific Aims themselves, Annette Rothermel cautions against having them depend on one another:

"Applicants shouldn't have aims build on each other since if one fails, the entire project may fail. Always have contingency plans, and design the project so that the aims work together but that one aim doesn’t require the 'success' of another."

A scientific review officer has this advice for investigators responding to a request for applications (RFA), though it applies to investigator-initiated applications too:

"There should be a simple testable hypothesis that is supported by preliminary data. Show preliminary data relevant to each aim and clearly tie the data to the aim (highlight your data when applicable)." —Frank DeSilva, Scientific Review Program (SRP)

For additional information, go to Choose a Testable Hypothesis and Draft Specific Aims to Test Your Hypothesis. Find links below.

Consider Other Critical Components

Here are some additional thoughts from SRP's Frank DeSilva on other key elements to ponder when designing your project (though his focus is on RFAs, the advice applies across the board). You'll need to address them all in your application to show that you've considered every angle.

"Demonstrate significance of your proposed work. Justify choice of methods and convince reviewers that you know your methods. If you don't, show that you've enlisted collaborators who can do what you propose. Describe potential pitfalls and alternative approaches, and address future directions."

Take Time to Consider Timing

An important part of designing your project is figuring how long it will take to complete. In tackling this step, many investigators tend to underestimate, so plan your research with the understanding that it may take more time than you might think.

To come up with an educated "guesstimate," consider as many actions or circumstances that will play into the amount of time you'll need for your project, start to finish.

Susan Brobst, a program officer in our Division of AIDS (DAIDS), suggests asking yourself questions, such as:

"Have you anticipated potential pitfalls and ways to overcome them? Have you considered the time needed to get samples from an off-site collaborator? If conducting human subjects research, do you have a contingency plan for accruing human subjects if you can’t meet your goals with the initial performance sites? Have you allowed sufficient time from when the last human subject is off the study and when the grant ends so that samples can be tested and data analyzed?"

As a planning tool, consider mapping out a timeline to visualize what you hope to accomplish in each year of your grant. Keep in mind that the most you can request for an R01 is five years, so it's crucial to assess whether you can do what you set out to in the limited number of years you ask for (which doesn't necessarily mean you'll get it). Moreover, you will likely be writing your renewal application before the first award period is over, so ask yourself where you will be at the time you need to write the next proposal. Will you have key data in hand by then?

With that in mind, having a timeline can give you a clearer picture of whether you're planning to do too much, as another program officer points out:

"New investigators in particular, are frequently criticized for being unrealistic and overly ambitious by proposing too much. Therefore, it helps greatly to prepare a detailed timeline which takes into account potential delays and the time it takes to repeat experiments. Applicants should also consider including a high-level version of this timeline (space-permitting) in the application."—Wolfgang Leitner

Bring In Collaborators

Quite likely, you'll need additional expertise to execute parts of your research. That's why you should carefully contemplate in what areas you'll need help and whom you'll choose to provide that help.

Think about this sooner than later as you design your project since identifying the need for additional expertise early on will give you adequate time to get feedback from those you seek out and to make adjustments.

Our participating program officers agree that if you have a gap in expertise somewhere, fill it with a collaborator. It's better to bring in reinforcements than to leave reviewers wondering why you didn't. That said, be sure a collaborator is truly that by having an active role in the research.

Annette Rothermel states:

"It’s a misstep not having a collaborator for an area of expertise that a PI doesn’t have documented evidence of mastering. However, it's important to have a collaborator who provides a strong letter of support, has assisted in the design of the proposed work, and reviews what is written in the grant application. Reviewers will question whether there’s a real collaboration if they find a disconnect between the stated collaboration and flaws in the project design."

If you think that bringing in collaborators will be seen as a weakness, think again. In fact, trying to do everything yourself may be more detrimental than having others take an active part in your project. Wolfgang Leitner offers some insight:

"Investigators, especially those who are new, should not try to do everything 'in house' in an attempt to demonstrate independence. They should not hesitate to recruit collaborators for different aspects of the project, or at least consultants who are willing to assist intellectually with aspects for which applicants do not have well documented (i.e., publications) expertise. In any case, it's crucial that investigators clearly describe the roles and contributions of collaborators and consultants."

DAIDS' Sue Brobst provides a warning worth heeding while also stressing the importance of addressing collaborators' roles:

"Avoid name dropping. Don’t include senior-level collaborators thinking their name alone will aid your project. This can backfire on you if their role isn’t apparent to reviewers. Be clear about the level of involvement, expertise, and role played by the people named in your application.

Also, get feedback from the collaborators. If reviewers find flaws in the design, they’ll check to see whether appropriate expertise was involved."

For Clinical Research, Consider the Scope

If you're interested in proposing a clinical research project or responding to a clinical research RFA, consider the scope of the project. Sometimes, what you or an institutional review board considers clinical or human subjects research may actually be a clinical trial. Since NIH's definition of a clinical trial is very broad, you should get clarification from a program officer.

Designing a project that involves a clinical trial has many facets, so you should have experienced clinical investigators, physicians, biostatisticians, and project managers on your team. Before getting too deep into your proposed project, we recommend talking to a program officer or others who are knowledgeable about this area.

Note that NIAID supports investigator-initiated clinical trials through planning grants (R34), implementation grants (R01), or implementation cooperative agreements (U01) using a defined policy and process. For more information, see Investigator-Initiated Clinical Trial Resources, below.

Related Links

Poor Writing and Presentation

Faltering in writing and presentation could turn your reviewers off from reading the application you've spent much time and effort preparing. See what stumbling blocks you could run into and how to steer clear of them.

First, Know Your "Limits" and Other Requirements

Before putting pen to paper, so to speak, get to know rules for page limits, font, margin and font size, and other specifications. That way you'll know how much space you have to convey the essentials of your project and how much you'll have to winnow the amount of information you have.

Both the eRA Commons (for electronic submission) and NIH staff check for page limits and formatting. Learn more at Does eRA electronically enforce page limits? and NIH Checks Your Application, linked below.

NIH may not review your application if you don't meet requirements, so it's best to make sure what you're allowed by reading instructions for your funding opportunity announcement (FOA). For R01s and other grant types that use electronic submission, follow instructions in both the SF 424 Application Guide and the NIH Guide notice. If the two differ, go with the Guide notice since it reflects the most up-to-date information.

For the number of pages you can use for different application sections, also check NIH's Table of Page Limits.

If you're responding to an institute-specific program announcement or request for applications, you must also pay attention to the initiative's objectives and special requirements. Should our program staff determine that your application is not responsive to the announcement, your application will not be reviewed.

One of our scientific review officers emphasizes the importance of reading announcements carefully:

"Applications are sometimes nonresponsive because investigators don't take time to read about the essential components, which results in a lot of time spent writing aspects of the application that may not be relevant or responsive to the initiative. When uncertain about responsiveness, applicants should talk with the program officer listed in the FOA for clarity."—Frank DeSilva, Scientific Review Program

No Getting Around Page Limits

You should not attempt to get around page restrictions. Since NIH is on the lookout, you could be penalized.

Alec Ritchie, a program officer in our Division of Microbiology and Infectious Diseases (DMID), has some general advice on what not to do:

"Applicants should not reference extra-application sources of information (e.g., FDA guidance sheet, company press releases, manuals) to circumvent page limitations. They should also avoid including Web links since reviewers are instructed to not click on them. One can argue that no information in the application should be dependent on material that isn't in the application, with the exception perhaps of publications."

Don't Misuse the Appendix

If you're contemplating circumventing page limits by including in the Appendix information that doesn't belong there, think again. You run the risk of possibly having your application pulled from peer review and funding consideration.

NIH clearly states the following in an April 2010 Guide notice (find the link below):

"Applicants...are prohibited from using the Appendix to circumvent page limitations in the Research Plan, such as the single page limit for Specific Aims or the specified page limit for the Research Strategy. If inappropriate material is included in an appendix (e.g., an extension of the Specific Aims or Research Strategy section) then the scientific review officer will instruct peer reviewers not to read or consider the material in their review of the application. In particularly egregious cases NIH has the authority to withdraw the application from review or consideration for funding."

One of our program officers highlights another downside to getting around page limits using the Appendix:

"Too often investigators will add extra material into the Appendix. Reviewers are often overburdened and not interested in taking that extra step to find what has been added. This leads to frustration for both reviewers and applicants."—Michael Minnicozzi, Division of Allergy, Immunology, and Transplantation (DAIT)

Rights and Wrongs of Writing

Whether you're a strong writer or not, the following tips should be helpful as you compose your application. For more information, go to Part 3. Write Your Application, linked below.

Know Whom You're Addressing

No matter what you're writing, be it a newsletter article or grant application, you need to know who your audience is so you can address them appropriately by using the right elements like tone and terminology.

The primary audience for your application is your scientific review group, composed of about 20 reviewers. Three people—the primary and secondary reviewers plus an additional reader—will have expertise closest to your field and will read your application thoroughly.

Note that not all members will have the same expertise or knowledge of your science. Therefore, it's best to write in such a way that all reviewers will understand your project's objectives.

For more on this, read Know Your Audience in the Strategy for NIH Funding, linked below.

Frank DeSilva has additional tips:

"Being concise is important. Spoon-feeding is optimal. Repetition is good but do not overuse it. In addition to the Specific Aims and Research Plan, make sure to follow guidelines for the biosketch, letters of support, resource sharing plans, and other items since these in sum will generally leave an impression of good grantsmanship and a well written application."

And Susan Brobst, a program officer in our Division of AIDS (DAIDS), offers this advice:

"Applicants should include key take-home messages in the application after presenting (or citing) preliminary data. That way a reviewer who is less familiar with the field can better understand the rationale for the study. This is critical for multidisciplinary applications."

Avoid Typos, Grammar Mistakes

When it comes to spelling and grammar, dot the i's and cross the t's—literally and figuratively. Having typos and bad grammar can interrupt the flow of your text and trip up readers. And when those readers are peer reviewers, you want to make sure nothing gets in the way of their perusing your application with ease.

Be careful not to submit an application riddled with spelling or grammatical errors. Two program officers tell you why:

"Typing and grammatical errors and similar 'minor' issues imply an insufficient attention to details that leads many reviewers to question the quality of the research being conducted in the applicant's lab. Therefore, proofreading for style, grammar, and formatting is crucial."—Wolfgang Leitner, program officer, Division of Allergy, Immunology, and Transplantation (DAIT)

"Improper spelling and grammar in an application tend to reduce reviewer enthusiasm and perceived potential for success, likely resulting in a score comparable to one of lesser technical merit and likely outside the competitive funding range."—Alec Ritchie

Provide Explanations or Justifications

You can also make life easier for reviewers by spelling things out for them, for example, if your research involves human subjects. Here's what we mean:

"When applicants believe their human subjects research is 'exempt,' they should clearly provide up front a justification or any human subjects information relevant to review. They should not leave it to reviewers to determine or agree that the research is exempt."—Alec Ritchie

Susan Brobst gives another human subjects-related example:

"Applicants often provide insufficient information for the use of human data or biological specimens that doesn't meet the definition of human subjects research. It's not sufficient to indicate 'No Human Subjects Research Proposed.' Applicants must explain why the proposed studies do not constitute research involving human subjects."

It's (Almost) All in the Presentation

Looks aren't everything, but they're definitely something when it comes to your application. Make your reviewers want to read it by making it visually appealing: neat, well organized, and easy-to-read. They'll appreciate the effort, especially since they have so many applications to evaluate.

Here's how to help your application make a good impression.

"Make effective (but judicious) use of bold, CAPITALS, and underlining as well as headers to clearly define sections. Insert figures and flow charts to explain experimental design where appropriate in the application."—Frank DeSilva

In addition to figures and flow charts, use other visual elements like tables to clarify potentially confusing points, as Susan Brobst says:

"If research proposed in the grant application is for a substudy of work supported under another mechanism, consider the use of a table to illustrate which aspects are supported by the grant application and which are supported otherwise. This reduces the chance reviewers will be confused and indicate your application is overly ambitious, has an inadequate budget, etc."

Wolfgang Leitner has a tip for investigators who may have a lot of data to share:

"Rather than squeezing countless multi-panel figures into the application, publish first before submitting. It frees up space and increases the 'credibility' of the proposal. The added benefit frequently justifies skipping a submission cycle in order to get your papers out."

Investigators who are resubmitting have additional details to pay attention to:

"For resubmissions, allow time to go through and update numbering for references, figures, and tables. Reviewers get annoyed when hunting for a Figure 4 that no longer exists or when Reference 75 does not contain the experimental details that the Approach section indicated. Ensure the letters of support are updated to reflect the revised application. It causes confusion when a letter of support refers to work that is no longer proposed. Likewise, review the budget and budget justification to ensure they reflect the revised application."—Susan Brobst

Find more information on presentation in Master the Application, linked below.

Don't "Overpack"

To keep your application appealing, give it "breathing room." That is, don't try to fit too much in the allotted amount of space. Doing so will result in pages that are filled to the brim with text or figures, which makes them user un-friendly and could ultimately be a strike against you at peer review.

The secret to not overpacking is to determine what you absolutely need to include; in other words, focus on the essentials, as Alec Ritchie describes:

"Applicants can put too much information within the required page limits. They must prioritize the material and consider how efficiently a reviewer will get through and appreciate the information presented. An overly dense application will not fare well at review."

Wolfgang Leitner also speaks to the "density" issue:

"A frequent criticism of reviewers is that applications are 'too dense.' This is the result of applicants trying to pack too much information into the proposal, which makes it difficult to read. Consequently, much of the densely packaged information gets lost during review."

He continues with a warning for those thinking about making room for content by using a work-around that ultimately doesn't work:

"Do not decrease the font or shrink the size of figures to be able to make the proposal fit! Reviewers will not appreciate such tactics. If the figure is too small and difficult to read, the information it contains may end up not helping you make your case."

On a related note: frequently, in an attempt to crowd even more text and figures in an application, investigators leave out figure legends and axis labels for graphs. The undesirable result: reviewers who are frustrated and left guessing.

Get Others to Read and Review

After you've finished writing, ask people—including nonscientists—to read your draft, especially if you are new to grant writing. Getting their fresh perspective is invaluable since they may spot issues you missed.

Alec Ritchie points out why getting readers is important:

"Having colleagues and collaborators review and critique an application before submission is essential. It's fairly obvious when this has not occurred and will not bode well for the applicant."

While you should get readers who are part of your project, it's a good idea to also recruit people without ties to your application. Wolfgang Leitner states:

"Ask colleagues who are involved in the project as well as those who aren't (and ideally know little or nothing about it) to read the proposal. However, keep in mind that people who are intimately familiar with the project may not notice flaws in arguments or that the proposal is hard to read."

Related Links

Information and policy on page limits

Last Updated July 17, 2013

Last Reviewed July 17, 2013