In my 10 years as editor-in-chief of JACC: Cardiovascular Interventions, we have selected about 1500 original research articles for publication. In recent years, the acceptance rate has been around 9%, so the editors have had to be very selective. Papers with high enough priority to be published in the journal have certain characteristics that I will describe in this chapter. There are, however, several other fine journals concentrating on publishing articles specific to interventional cardiology, and some of them have different interests. Also, general cardiology journals and the most selective medical journals also publish interventional cardiovascular papers. So the thought when preparing a research paper should not be, “Will it get published?” but, instead, “Which journal is best suited for my submission?” The answer to that question usually lies in the project itself. A well-planned research project will almost always result in a publishable paper. Knowledge of the type of papers published in each journal will aid in deciding where to send the paper.

When I assumed the role of editor-in-chief of JACC: Cardiovascular Interventions and associate editor of JACC, Tony DeMaria, the editor-in-chief of JACC, had stimulated the associate editors to reflect on how to get a paper published in a highly rated journal.^1,2 I have modified those ideas over the years and will give you my advice as to what interventional cardiology journals are looking for. The first principle is the project itself. Without a well-planned research project, a publishable paper cannot be written. So what are the fundamental characteristics of an excellent research paper?

The 3 characteristics that editors are looking for in a research paper are novelty, accuracy, and importance. This thought process of “Is it new, true, and relevant?” goes through the mind of reviewers as well. Perhaps even before these characteristics are considered, the question “Is it interesting?” is entertained. Since the job of editors and reviewers is primarily to select papers that qualify for their journal, one should not underestimate the impact of the first impression. Is it interesting or not?

Novelty

If the question being addressed has not been studied before, then it is ranked highly as novel. There are, of course, levels of novelty, and all authors attempt to justify why the project was undertaken. If the investigation has been done, then it should address what needs to be done in addition. Is it a much larger series or a comparison that confirms prior inadequately powered communications? Does it address a unique application or a unique population that has not been adequately studied? Numerous papers submitted to the journal are sometimes directed toward subsets of large pivotal trials. If these were not reported in the main paper, and especially if prespecified and addressing interesting questions, they are considered to have some novelty.

Accuracy

Is the question addressed in a way that the answers will be true? This does not mean that the findings of the investigation will reflect ultimate truth. No scientific study can claim that, but the findings must be accurate as they relate to the study. The study group characteristics and the protocol are critical components. It is not my interest here to provide a thesis on methodology for designing and performing research or on statistical methods that are valid for various investigations. However, power calculations must be considered. Here, the input of experts in statistical methods should be encouraged. The methods must be capable of withstanding scrutiny, and they should be validated and reproducible as shown by prior work. They should be as precise as possible, and this will vary based on the data sources that are available for the work. Prospectively collected data are usually superior, but precision in the collection of those data, as well as in collecting retrospective data, is important in judging the validity of a study. Confounding variables can seldom be completely eliminated but must be considered and minimized. Randomization is assumed to remove confounding but does not always do so, and for nonrandomized comparisons, unrecognized confounders are important to consider. When results of nonrandomized comparisons seem too good to be true, the cause is commonly the presence of systematic confounders that cannot be accounted for. We may find that “The sicker patients did worse,” but we may not have identified why they were at greater risk.

Importance

The relevance of studies carries a lot of weight when considering publication. Importance of a study is usually viewed in a hierarchical ranking. At the top are things that have implications for patient management. When that reaches the level of potentially changing practice, the highest level of importance has been reached. Areas of relevant importance include when studies establish diagnoses, quantify severity or risk, or define mechanisms by which outcomes are determined. Even when the study is not adequate to establish any of these but generates a novel hypothesis, the paper may be of interest. However, it is true that the statement “This paper is only hypothesis generating” is frequently part of the review of a rejected paper. If the study fails to provide more than a hypothesis for further study, that should be indicated rather than insinuating that the paper answers important questions. In that case, the importance of the hypothesis and the strength of evidence pointing to why it should be studied will be helpful. Finally, even if a study is well done, but the result is not important at all, one should wonder why it was initiated. At an editorial board meeting, when an associate editor discussing a paper says, “So what,” it is a very damaging comment. The methods may have been correct, but the finding is not important.

I said that a well-planned project usually results in a publishable paper, and I would reemphasize that 90% of a successful paper lies with the planning and execution of the project. Before initiating a study, several questions must be considered. First, identify the question. Then, make sure it has not already been answered. Having a patient base available is not in itself a reason to initiate a project. The question should precede the resources to address it. Then a hypothesis must be generated. Consider the type of study that might address the issue. Some questions cannot be answered without a randomized comparison, while others can. Evaluate whether the resources are available to conduct the study. Is the patient base adequate at 1 institution, or are collaborations necessary? Can a database be accessed, and what is the quality of those data? Consider personnel and financial resources for the study. The final question that should be asked is: “Will the product that is produced be worth the effort that will be necessary?” This is not to say that the answers are predictable; if so, the research is not needed. However, are the question and whatever answers may be obtained interesting?