Can Publication Targets Encourage Researchers to Ask Smaller but Less Important Questions?

Can Pressure to Publish More Change the Questions Researchers Choose to Ask?

Suppose two research projects are available. One addresses a difficult problem that may require three years of data collection and could produce one substantial paper. The other consists of several narrower studies that can each be completed within a few months and are likely to generate multiple publications.

If your institution expects a certain number of publications every year, which project becomes easier to justify?

That is one of the less obvious effects of publication targets. They do not merely influence how much researchers publish after research has been completed. They can influence what researchers decide to investigate before a study begins.

A publication target may encourage researchers to complete and disseminate work, which can be beneficial. But if researchers must repeatedly demonstrate productivity through publication counts, they may also have a reason to prefer questions that can be answered, written, and published quickly. The result can be a subtle shift from asking, “What question is most worth answering?” toward asking, “What question can reliably produce an output?”

Yes, but the Effect Is Not Automatic

Publication Targets Can Affect Research Before Anything Is Published

Publication quantity is easier to count than research importance

Institutions need ways to evaluate research activity. Publications are visible, verifiable outputs, so publication records commonly enter hiring, promotion, performance review, and other forms of academic assessment.

The difficulty is that publication count and research importance answer different questions. A count tells you how many outputs were produced under a particular counting rule. It does not tell you, by itself, whether those outputs addressed consequential questions, used appropriate methods, substantially advanced knowledge, or produced findings that matter beyond academia.

This distinction becomes important when researchers know that a particular number of publications will affect promotion, workload, incentives, continued appointment, or professional recognition.

A healthy assessment system would not require these considerations to conflict. But when output quantity carries substantial consequences, publication yield can become part of project selection whether or not anyone explicitly tells researchers to choose smaller questions.

Annual targets can disadvantage questions with long research cycles

Research questions do not operate on uniform timelines. Some can be investigated with existing datasets or short experiments. Others require longitudinal observation, prolonged fieldwork, repeated measurements, complex recruitment, development of new methods, access to rare populations, or years of theoretical work.

An annual publication target creates a particular temporal logic. Researchers need outputs within the assessment period.

A three-year project may be scientifically defensible and potentially consequential, yet provide little immediate evidence of productivity during its early stages. Several shorter projects may produce visible outputs every year. When assessment repeatedly rewards the latter, researchers may have a practical reason to maintain a portfolio of projects capable of generating publications on schedule.

That does not prove that researchers will abandon long-term work. It does show why the structure of the incentive can affect which research risks appear professionally affordable.

Smaller questions are not necessarily lesser questions

Size is a poor proxy for importance. A tightly focused study can resolve a consequential uncertainty. A large, expensive, multi-year project can ask an uninteresting question. Some research problems are best decomposed into narrower questions because careful cumulative investigation is scientifically appropriate.

The problem is therefore not that researchers ask small questions.

The concern arises when questions are made smaller primarily because the reward system values the number or timing of outputs. The relevant comparison is not “small versus large,” but “appropriate scope versus incentive-driven scope.”

One project can legitimately produce several papers

Complex projects often contain several distinct research questions. A longitudinal dataset, clinical trial, large survey, or multidisciplinary program may appropriately support multiple publications when each paper addresses a sufficiently distinct question and the relationship among outputs is transparently reported.

This should be distinguished from excessive fragmentation, sometimes described as “salami slicing” or publication of least publishable units. In that situation, closely related findings that might form a coherent contribution are divided primarily to increase publication count.

Concerns about such practices are longstanding. The National Academies' discussion of responsible scientific practice identified overemphasis on short-term projects and organization of research communication around the “least publishable unit” as potential consequences of systems that reward quantity and speed.

More recent literature has likewise criticized excessive fragmentation because it can create redundant or overlapping publications and make the scientific record harder to interpret. However, empirical evidence does not justify assuming that publication pressure has caused universal increases in salami slicing. A large bibliometric analysis by Fanelli and Larivière found that, after accounting for increasing co-authorship, individual publication rates had not simply risen across the twentieth century as common narratives about publish-or-perish pressure might suggest.

The appropriate conclusion is therefore cautious: the incentive exists and fragmentation is a recognized concern, but publication counts alone cannot tell you how frequently researchers respond by dividing their work.

Publication pressure may encourage predictable questions rather than merely small ones

Another consequence concerns uncertainty. Important research can fail. A promising hypothesis may not be supported. Recruitment may take longer than expected. A difficult methodological problem may resist solution. A new line of inquiry may require several unsuccessful attempts before it becomes productive.

If researchers need regular publications, projects with uncertain timelines become professionally costly. A safer project may be one with accessible data, familiar methods, predictable analyses, and a clear route to a manuscript.

This does not make the resulting research worthless. Incremental research is essential to cumulative knowledge. Yet a system that disproportionately rewards predictable output may discourage some forms of intellectual risk even when those risks are scientifically justified.

The incentive can operate without anyone consciously choosing “quantity over quality”

Researchers do not need to think, “I will conduct less important research so I can publish more.” The adjustment can be much subtler.

A researcher may decide that a longitudinal design is unrealistic given promotion timelines. Another may select an existing dataset instead of collecting evidence needed to answer a more ambitious question. A doctoral supervisor may recommend a safer project because the student needs publications before graduation. A team may divide its research program into projects that fit annual reporting cycles.

Each decision can appear reasonable in isolation. Collectively, they illustrate how a research incentive can begin distorting the activity it was intended to encourage.

Publication pressure and poor research are related concerns, but not synonyms

Studies of publication pressure have reported concerns among researchers about environments in which publication records strongly affect academic careers. Research in Amsterdam across disciplinary fields, for example, found negative attitudes toward the prevailing publication climate and particularly high perceived publication stress among postdoctoral researchers and assistant professors.

Other scholarship has linked publish-or-perish systems conceptually or empirically with questionable publication practices. Still, causal claims should be made carefully. Researcher behavior is influenced by funding, employment conditions, disciplinary norms, collaboration, journal practices, available infrastructure, personal motivation, and other factors alongside publication expectations.

Publication targets should therefore be treated as one potentially influential part of the research environment, not as a universal explanation for weak research.

Responsible assessment tries to reduce dependence on simple output counts

The San Francisco Declaration on Research Assessment (DORA) argues for evaluating research on its own merits rather than relying inappropriately on journal-based metrics, while the Coalition for Advancing Research Assessment (CoARA) calls for assessment that recognizes diverse research contributions and relies primarily on qualitative judgment supported by responsible quantitative indicators.

These approaches do not require institutions to stop caring whether researchers publish. Dissemination remains a fundamental part of scholarship. The more consequential question is whether assessment gives researchers enough room to pursue work whose value cannot be represented adequately by how many papers it produces within a reporting period.

When a Publication Target Changes Which Project Looks Rational

The example does not establish that Option A is inherently better. Perhaps the longitudinal project is poorly designed, while one of the smaller studies addresses an urgent problem elegantly. The point is that publication targets introduce an additional criterion into project selection: how reliably and how soon will the project produce countable outputs?

Common Misunderstandings About Publication Targets and Research Questions

Ask Whether the Research Problem or the Output Target Is Setting the Scope

If you work under publication expectations, pretending those expectations do not matter is unlikely to be useful. Career constraints are real. The practical task is to recognize when they are beginning to determine the substance of your research.

One useful test is to imagine that publication count disappears from your evaluation. Would you still divide the project in the same way? Would you still choose the same research question? Would the same scope make scientific or scholarly sense?

If the answer changes substantially, the incentive is probably influencing your decision. That does not automatically make the decision wrong. It tells you that the trade-off deserves conscious evaluation rather than being mistaken for a purely intellectual choice.

The broader issue is closely connected to what happens when publishing itself becomes the goal rather than the research. Once producing another paper becomes the primary unit of success, questions can begin to be designed around publications rather than publications around questions.

Before Shrinking or Splitting a Research Question for Publication

Questions About Publication Targets and Research Scope

Do Not Let the Number of Papers Determine the Size of the Question

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