Grant Writing. A Homily
PREPARING A GRANT PROPOSAL. A HOMILY,
A homily is a sermon intended to edify a practical matter.
Oxford English Dictionary
Mayo Professor Emeritus
Questions to ask yourself and obvious things to consider at the outset:
What types of studies have already been carried out on the question?
What was their quality and place in the hierarchy of causal inference?
What are the gaps in knowledge that require to be filled?
What is the appropriate research strategy toward filling the gaps?
Can causation be inferred from current knowledge taken all together?
If so, what questions remain and what preventive research strategies are indicated?
I. Know the literature
Know your subject in its historical perspective.
See your idea in the context of a continuum of ideas.
Know who is now working on the issues and how they are exploring them.
Know the present state of knowledge on the question.
Be familiar with scholarly reviews as well as empiric studies.
Be precise about the global importance of the subject.
Present a systematic review of the literature that is both exhaustive and scientifically critical, giving strengths and limitations of the studies reported.
Rank them for quality within the hierarchy of causal inference.
Make your own (statistical?) summary of the sound studies.
Review the critical literature succinctly in your proposal.
II. Stage of Knowledge
Your understanding of the literature, through its critical review in the proposal, should indicate that you have a clear picture of the stage of knowledge. This understanding, in turn, predetermines the appropriate study method for your proposal as well as your study hypotheses and specific aims. Your demonstrated knowledge of the literature and of the present state of explorations of the subject is central to convincing your peers of the importance of the issue and of the overall worth of your proposal.
III. State the Question Clearly
Propose specific hypotheses, preferably in traditional format.
Present questions in a succinct and unambiguous manner appropriate to the analyses proposed.
Limit the number of your scientific questions and of the specific aims. [Avoid taking on all possible questions at once, or trying to propose the perfect study. “Don’t let the best be the enemy of the good.”]
One good question can create a lifetime career in which that one question leads to another and then another. Good performance in the study of one question creates a track record and often gives the opportunity to look at the next question.
IV. Seek Consultation
Armed with a firm knowledge of the background, the stage of knowledge, and the importance of your question, and with the draft of a focused proposal in hand, test your idea with experienced people. With their help try to tear your idea apart so that you may build it back stronger.
Feasibility is almost as important in epidemiology as is the scientific question itself. Feasibility is more important than in clinical and laboratory research because of the greater scope, duration, and cost of most epidemiological research. Moreover, the questions in epidemiology are usually broader, the differences sought are often smaller, and the confounding factors and study conditions are always more complex. In addition, the measurements in epidemiology are less precise and the time required to gather data greater than in other forms of research.
Thus, you will do well to limit your questions, focus sharply, and make a strong case that your study is “do-able,” that is, its aims are attainable within the grant period proposed.
[There is no more effective proposal than one resulting in study section reviewers volunteering this sort of comment: “This question can probably be answered by this group within the time and costs proposed,” in contrast to the comment: “This is an important question and a good group, but they may have bitten off more than they can chew. It is unlikely they can answer this question by this proposal.”]
VI. Background of the Investigator
Reviewers will consider your track record as well as the facilities, the study populations available, and the resources at your institution. Strive to present this strongly but, I suggest, without grossly “tooting your own horn.” It is best to stick to the facts and to avoid superlatives in describing your own contributions. [Reviewers may be turned off by use of terms such as these: “We have a history of “successful,” “salient,” or “cutting-edge” research.]
I suggest that it is wise to have a senior person with a good track record as co-principal or co-investigator or consultant to your project. It lends weight.
It is desirable as well that you have hands-on field experience such as a Project Officer obtains before proposing yourself as a principal investigator. At Minnesota, we recommend and support a full post-doctoral training program for young investigators as the more natural and effective way to participate in research before entering a field and shouldering the full responsibility of independent investigator.
Credible experience requires that you “walk before you run,” that you participate as part of a team before you lead one, that you get a small grant before you seek a substantial R01, or that you get a career-development award or sign on to another’s project as co-investigator or project officer before seeking to be a principal investigator.
Finally, reviewers will weigh your creativity, tenacity, and judgment along with the demonstrated support of your institution.
VII. Significance of the research.
Significance of the question, a standard segment of the NIH application form, is the place where you display your idea in context and within the historical continuum of ideas, where you give evidence of understanding the issue and the potential impact of answering the question. Your objective is to convince others who work in the field that you are not only capable but that “you mean business.” [It may help to consider the traditional admonition: “what is not worth doing, is not worth doing well!” In other words, one should avoid spending a life vigorously pursuing questions that are not worth asking in the first place. Each of us needs external advice here.]
Your project will be judged particularly for its significance, interest, novelty, and relevance, and for its ethics and feasibility.
Clarity, style, language, and organization of the proposal are integrally linked with the ideas themselves. Some consider that good writing is just a “knack,” a desirable but unessential part of a research career, and that good language and syntax are details or luxuries less important than the ideas themselves. In fact, language is the main external indicator of the quality of thought.
Good language not only indicates your respect for ideas, it shows reviewers your care for detail and confirms your diligence and even says much about your character. Writing skills should be honed. Research skills develop over time; so can writing skills. Do not hesitate to seek editorial as well as scientific consultation. Copy edit, then reedit, then have colleagues review,then reedit, and finally, proof-read carefully.[I recommend two style manuals as particularly useful: “Stunk and White,” and “The Chicago Manual of Style” as well as familiarity with “NIH guidelines.”]
IX. Specific Aims
State hypotheses clearly. This section of a proposal expresses clearly the originality of your thinking as well as the feasibility of the study. Hypotheses are best stated in the traditionally succinct manner, either positively, or as a formal test of the null hypothesis (“– that there is no difference –”).
Specific aims should be in the format of a short list with a minimum of narrative support. The aims should tell exactly what you are going to do and a precise schedule for doing it.
X. Organization of the proposal
Consult carefully and early all instructions available from the appropriate agency for your type of grant, including page limits and the format for references. Your proposal needs to be professional in form, orderly, and flowing, contained in a neat and attractive but not commercially “slick” presentation. Flow is enhanced by putting details in footnotes or appendices.
A good editor and copy editor are as essential for grant proposals as for manuscripts. Even Hemingway needed and employed an editor. A proposal that is ponderous, poorly organized, sloppily constructed, full of dull syntax, or containing any grammatical errors or typos, reflects negatively on the care, seriousness, and capability of the proposer. Failures may even be considered an insult by peers who give their time and effort to review your proposal.
XI. In Epidemiology, “We are #3; we try harder!”
Epidemiology is a “minority” academic profession. Most scientific questions in medicine derive from clinical observations or laboratory science. In population studies new questions are few. We are dealing neither with the “baroque beauty of biology” nor with fundamental biomechanisms; we deal with numbers, estimates, probabilities, and inference of causation. Thus, we are rarely able to impress peers with brilliant ideas about underlying causes. Rather, we must convince them by our breadth of understanding, clarity of thought, and mastery of epidemiological methods.
For example, we present a priori hypotheses, computations of sample size, and power estimates of the probability of detecting an effect. We can describe our multi-disciplinary teams, their vigor and credibility, and we can show care in documentation of resources and facilities. We can justify the budgets we propose, including generous cost-sharing of faculty effort to demonstrate institutional support. We can show adequacy of technical staffing and document effectively our experience in research administration and in recruitment of subjects. We can convince reviewers by the elegant analyses we propose, the unique populations we can represent, and by our record of the persistent, orderly pursuit of important issues in the public health. Finally, we can impress peers by the excellence of our presentation and by its feasibility and potential for getting an answer within the prescribed time and cost.
XII. Pilot Studies
What is the evidence for the feasibility of your research?
The most convincing evidence is your own experience of testing its methods and schedules and recruitment, whether to a survey or to treatment modes. Small-grant mechanisms are useful for such pilot studies.
XIII. Know the New NIH Rules and Guidelines
Current NIH Review Criteria are important to know but they may be vague and amenable to discriminatory application. For example, they ask the following rather subjective questions:
“Does the study address an important problem?
How will scientific knowledge be advanced?
[In fact, importance is in the eye of the beholder. I am reminded of the clinical scientist who confronted me at NHLBI one day with the comment: “Epidemiology has made its contribution. Now we are concerned with more interesting and important things.”]
Are the conceptual framework, design, methods, and analyses adequately developed, well-integrated, and appropriate to the aims of the project? Does the applicant acknowledge the potential problem areas in carrying out the project and consider alternative tactics?
Does the project employ novel concepts, approaches, or methods? Are the aims original and innovative? Does the project challenge existing paradigms or develop new methodologies or technologies?
Is the investigator appropriately trained and well suited to carry out this work? Is the work proposed appropriate to the experience level of the principal investigator and the other researchers?
Does the scientific environment in which the work will be done contribute to the probability of success? Do the proposed studies take advantage of unique features of the environment or employ useful collaborative arrangements? Is there evidence of solid institutional support?”
The NIH Research Agenda
The President’s budget is likely to propose a small increase in NIH funding. NIH advisors have pointed out that NIH, this major center of national excellence and enterprise, should be strengthened, with the expectation that the return yield would be substantial for the health and economy of the country. The short-term result for investigators could be a small increase in dollar amounts available, some increase in the number of awards, and an improvement in the funding line for approved RO applications.
There also will continue to be more central control of epidemiological researches because they frequently exceed the $500,000 dollar line of policy review. Moreover, the vagueness of the new criteria for “importance,” and “innovation” of proposals may still be applied in a discriminatory fashion by staff and by the NIH Advisory Council. And the pendulum of NIH is not swinging toward population phenomena, social determinants of illness, and prevention, but is still strongly toward personallzed and high-tech medicine and care.
Consult the home page for details of current grant policy, for example, at the National Heart, Lung, and Blood Institute: http://www.nhlbi.nih.gov/nhlbi.htm
XIV. Red flags
Avoid the following red flags for reviewers:
Exposing your pet opinions unnecessarily.
Irritating folks by vagueness of expression, diffuseness of scope, or by “fat” in your budget. [Review groups are particularly critical of large costs for travel, equipment, consultants, research associates, and for a large percent effort for the PI. This effort should be as substantial as possible while the funding support requested is as low as possible, thus demonstrating institutional support.]
Requesting too little as well as too much support for data processing and computer time or for quality control and technical help.
Presenting a sloppy proposal, or its extreme opposite, a super-slick, “commercial” proposal (bound in plastic with multiple colors!).
An academic career will be happier, and grant-writing healthier, if the grant deadline is anticipated by a week or two. By avoiding repetitive brinksmanship you will be supported more effectively and willingly by your staff, colleagues, director, dean, and central research administration (not to speak of reducing tension at home).
XVI. IRB Approval
The current situation of institutional review is rife with problems, acute and chronic, due to the heavy IRB work load and the rapid flux in national and local privacy and consent policies and regulations. Sadly, there is another problem, a lack of comprehension among most IRB faculty of the elements of population-based research or an appropriate regard for the population as a laboratory and for epidemiologic research, in general. [Serve whenever possible on your institution’s IRB to influence this culture.]
XVII. Today’s Grant Culture
Despite the relatively disadvantageous position of epidemiological proposals due to their cost and program bias, there is cause for optimism. Good ideas presented in well-constructed proposals by sound investigators are often eventually funded. [Like cream, they rise to the top. But unlike cream, they don’t rise unassisted. It takes energy and persistence.]
Keep in mind that good questions presented in clear proposals will usually, eventually, fly. The NIH Epidemiology and Disease Control study sections, for example, are always delighted to receive, and are highly responsive to well-structured, short-term proposals costing $50,000 to $250,000 a year. Moreover, a grant of such magnitude requires no policy and program review by NIH Councils.
In addition to making every effort to reduce costs, innovation is increasingly important in today’s competitive climate. Even among peer review in the “our own” EDC Study section these days at NIH, the mood is “out with the old, in with the new;” the old is being labeled “macro-epidemiology,” even “circular” epidemiology (the circular study of similar risk factors). [Cynically, the new, of course, is called genetic or molecular epidemiology.]
Emphasize what is unique, specific, and innovative in your proposal.
[A little career advice:
NIH remains “the only game in town” for epidemiology, and a good track record at NIH is the only sound basis for an academic career in epidemiological research. One needs, nevertheless, to understand the constraints of NIH budgets and policy and adapt to them in making proposals.
Program priorities at NIH have swung to emphasis on molecular biology, requiring even greater effort in proposing and carrying out population-based researches. It demands a cohesive community of epidemiologists who can be persuasive in NIH, Congressional, and public forums.
For the young investigator, we recommend laying down a track record by working with strong people in a strong center. Experience as a post-doctoral fellow, as a young co-investigator, or as an RA, is the best preparation for going it on your own. NIH First Awards, for example, beget prestige and reputation, and provide a crucial period for maturation and apprenticeship. During this period, you get to know personally those experienced in your field and can make them aware of your skills in research and of your availability. Volunteer to serve on working groups, task forces, and national committees. It is useful also to accept and work diligently at opportunities for peer review or editing or consulting for journal articles and grants. In the early years you would do well to say “yes” to many such opportunities. In full career you will do well to say “no.”]
The self-help experts so popular in the business world have a few credos that may be appropriate to our profession; for example:
“Failure is a key to success.”
“Success is getting up after every fall.”
After your proposal is pummeled in the first round of review, get up off the floor and heed carefully what is said in criticism. Digest the “pink pages” carefully, talk about them with others, and resubmit with an acknowledgment of: “the positive contribution of this critical review to the strength of our proposal,” if such is the case.
Never give up. Two submissions are “par for the course,” three are common nowadays, four not unheard of. Courage, confidence, persistence, and resilience are part of the game.
XIX. The Peer Review System
Investigators can play a role in educating reviewers about their “cutting edge” issues. It is important to submit an idea early rather than late. Early submission usually expedites education of the peer review system to achieve eventually competent review of your innovations. It can require several years to “educate” a review system in a wholly new field, since innovative research is by definition not establishment research. The review establishment has to be brought up to speed. [For example, in the late 1970s, getting preventive trials and community and public health trials funded required several years for peer review to come up to standard in its skills and understanding of the new fields.]
XX. Personal Issues
First, Know Thyself!
An honest self-assessment of one’s personality, work habits, and competence is important on entering a career of investigation and on submitting proposals for research. Epidemiology is no place for fools. But it can be a good place for all others.
Know what drives you.
What basically challenges, pleases, and preoccupies you?
I like to consider that there are at least three kinds of people in our profession, idea people, doers, and methodologists. We seek to be all these. But are you primarily an idea person, reasoning, imaginative, having active fantasies, and fascinated with ideas? If this is your strength and contribution, you will always be needed and sought out, but there is a danger that you will become bored with details such as grant proposals and actual implementation of your ideas. Therefore, you may need to seek help in the actual writing of, or administration of grants. You will need to find colleagues with complementary skills of organization, “get-it-done” and “people” skills, to complement your good ideas.
Or are you primarily action-orientated, a “doer,” happy mainly when you are implementing things and being effective in organization and working with people and schedules? If so, your skills, too, will always be needed, and you, too, will be sought out, but you will need to work on your thinking, creativity, and imagination as well as trying to surround yourself with colleagues having complementary skills.
Are you primarily a person concerned with, and good at detail, method, and precision? If so, your contribution will always be sought, to devise procedures, criteria, schedules, methods, instruments, and standards. This can, in turn, result in substantial new contributions to knowledge and can even open up the possibility to ask new questions. But you will need to work as part of a team of people who complement your skills.
It is important to understand early your attributes and drives, your tendencies, for example, to be a loner or team worker, a planner or initiator, an optimist or a pessimist, open or closed-minded, suggestible or skeptical, patient or always in a hurry. Whatever your drives and attributes, seek to put yourself in a strong and reputable institutional setting, and then surround yourself with people who complement your skills. This will serve, in turn, to motivate you to perform beyond your skill and your natural tendencies. It will facilitate carrying out your ideas and developing a more useful, satisfying, and all-round “successful” career.
Know your basic competence and what you most like and want to do. Where you lack skills, you need to find colleagues who have those skills. Basically, however, one needs to stay in an area where one has the crucial basic elements of understanding, skill, experience, and passion, and where you find a certain level of comfort. It is painful and unhealthy to be always out on a limb, working beyond one’s competence, under constant threat of disaster.
How do you communicate?
Talking over your ideas with others, peers, colleagues, and senior people, should serve to boost and inspire you, though it may on occasion depress you. It helps you get to the nub of the scientific question and to evaluate the overall feasibility of answering your question.
Knowing firmly what you want to do with your life, and having career goals, are useful but I believe they are not essential to a good career. I have the impression that this may be a generational problem. Today, there are so many wonderful things “out there” that young people seem to have difficulty finding and focusing on a major thing they want. They want it all. Or they want to try it all.
I advise: Do well what’s in front of you!
The most important thing is to do very well what you have the opportunity to do now, even if at the moment you are not driven by overwhelming creativity and purpose in that task. In time, as they used to say about arranged marriages, the passion will come.
The essential, in my view, is commitment to do a good job of whatever you are doing. That practice almost invariably leads to opportunities to go on and do other good jobs. Perhaps “love” will develop later and your directions, goal, and “purpose in life” will clarify. But even if you experience no epiphany, are not “called,” or do not move onward and upward to some professional Nirvana, you will reap deep satisfactions and credibility if you have done each job well.
We in epidemiology and prevention research are fortunate to live in a field in which Nobel Prizes and the like are simply never awarded. Because we can never get one, we don’t need to worry about them. We only need the personal satisfaction and recognition of a few peers and friends for a job well done.
XXI. Know Thy Peers
In addition to knowing thyself, it is important to know thy peers. In my view, it is not vulgar grantsmanship, but rather professional courtesy and good sense, to familiarize yourself with the work of the people who will sit in judgment of your work. In every biomedical library, every dean’s office, and every research department head’s office, there is an annually updated directory of NIH Councils, study sections, and committees. Or check the NIH “gopher” for the appropriate website. If you don’t know which study section will handle your grant, call or write the Division of Research Grants at NIH with your grant number and they will refer you to the study section project officer from whom you can find detailed information. Look up the names of the study section members in the directory and do a library search on their contributions. You may learn something.
Good Grantsmanship! Good Hunting!
Henry Blackburn MD
Mayo Professor Emeritus
U. of Minnesota