Executive Summary
This paper develops the conceptual foundation for neglect studies as a distinct field of inquiry. It addresses three tasks. First, it establishes the scope of the field by specifying what counts as an instance of scholarly neglect and what does not, distinguishing genuine neglect from appropriate deprioritization. Second, it proposes a working taxonomy of seven categories of neglect — orphan topics, abandoned research programs, methodologically inaccessible questions, interstitial questions, peripheral inquiries, sensitive questions, and constituency-less questions — with the understanding that these categories overlap and that real cases often belong to several at once. Third, it traces the field’s intellectual antecedents in greater depth than the preface allowed, situating neglect studies in relation to agnotology, the sociology of undone science, metascience, priority-setting research, the research-waste literature, the history and philosophy of science, library and information science, and several smaller bodies of work that have addressed pieces of the same problem under different names.
The paper concludes with a discussion of boundary problems and an outline of the questions that the methodological paper (Paper 2) will need to answer if the field is to develop rigorous standards for its own claims.
1. Introduction
The preface to this series argued that the distribution of scholarly attention bears a complicated and often weak relationship to the distribution of scholarly importance, and that the institutional and intellectual scaffolding needed to study this phenomenon systematically has not yet been built. The argument was deliberately general. This paper undertakes the more difficult work of specifying what the field would actually study and how it would distinguish itself from adjacent enterprises.
The difficulty is genuine. A field whose subject matter is what other fields overlook faces three structural challenges that more conventionally defined disciplines do not. The first is that its object of study is defined negatively — by absence rather than presence — which complicates ordinary empirical methods. The second is that its claims are easy to make and difficult to substantiate, since asserting that something is neglected is rhetorically cheap and verifying the claim is methodologically expensive. The third is that the field’s boundaries are inherently porous: any topic could be argued to be neglected from some perspective, and without principled criteria the field risks becoming a venue for any scholar whose preferred questions are not receiving the attention they would like. The taxonomy and the antecedent discussion in this paper are intended to address the first and third of these challenges. The second is the work of Paper 2.
A note on terminology. The field’s eventual name remains an open question, and Paper 8 in this series returns to it. Neglect studies is used throughout the present series as a working term, with the understanding that alternatives — agnotology in an expanded sense, attention studies, epistemic gap analysis, undone-science studies — all carry their own implications and constituencies. The working term has the virtue of plain English and the cost of seeming to promise less methodological sophistication than the field aspires to. The trade-off is accepted for the duration of this series.
2. What Counts as Neglect
A working definition: scholarly neglect is the condition of a question, topic, population, method, region, or line of inquiry that receives substantially less sustained scholarly attention than would be warranted by its importance, tractability, or expected value if pursued, where the deficit in attention is attributable to mechanisms other than considered judgment about the relative merits of available research directions.
Three elements of this definition do significant work and deserve unpacking.
The first is substantially less. Neglect studies is not concerned with marginal differences in attention across topics; the distribution of research effort will always be uneven, and the field’s claim is not that the distribution should be uniform. The claim is that some deficits in attention are large enough, and the topics important enough, that the gap merits study and, where appropriate, intervention. What counts as substantial is a methodological problem rather than a definitional one, and Paper 2 takes it up.
The second is importance, tractability, or expected value. These are three separate grounds for thinking that a question merits attention, and they can come apart. A question may be important without being tractable, in which case its neglect may be appropriate until enabling tools arrive. A question may be tractable without being important, in which case its neglect is unproblematic. A question may have high expected value — meaning that the product of its importance, its tractability, and the probability of useful findings is high — without being either spectacularly important or trivially tractable. The field’s interest is in questions that score reasonably well on at least one of these dimensions and that nonetheless receive little attention.
The third is attributable to mechanisms other than considered judgment. This is the most contested part of the definition. The field is not interested in cases where research communities have deliberately and reflectively concluded that a question is not worth pursuing; those cases are simply the ordinary work of disciplinary prioritization. It is interested in cases where the deficit in attention is produced by mechanisms — funding incentives, prestige hierarchies, methodological habits, political sensitivities, disciplinary boundaries, historical contingency — that operate without anyone having considered the question on its merits. The distinction is difficult to draw in practice, since the boundary between considered judgment and structural neglect is rarely clean. But the distinction does real work, because it focuses the field on cases where intervention is plausibly justified rather than on cases where intervention would be presumptuous.
The definition explicitly excludes several phenomena that might seem related. It excludes mere unfashionability, which is a feature of all intellectual communities and not by itself a problem. It excludes the ordinary lag between a question being identified and a research community forming around it. It excludes the appropriate concentration of effort that follows from genuine theoretical progress, where research clusters around productive paradigms because they are productive. And it excludes the misallocation of effort within active research programs, which is the territory of the research-waste literature rather than of neglect studies proper.
3. A Working Taxonomy
The taxonomy below proposes seven categories of neglect. The categories are not mutually exclusive, and the most important cases for the field tend to belong to several at once. The point of the taxonomy is not to assign each case to a single bin but to clarify the different mechanisms by which attention fails to reach a question, since different mechanisms call for different institutional responses.
3.1 Orphan Topics
An orphan topic is a question or area of inquiry that has no sustained research community — no graduate programs producing specialists, no journals devoted to it, no conferences organized around it, no senior scholars who identify it as their primary research interest. Orphan topics are not necessarily unstudied; they may receive occasional attention from scholars whose primary identification lies elsewhere. But they lack the institutional infrastructure that allows knowledge to accumulate cumulatively rather than episodically.
The orphan-topic category includes both topics that have never had a community and topics that have lost the one they had. The latter shades into the second category, abandoned research programs, and the two are sometimes difficult to separate. The distinction is roughly that orphan topics are characterized by the absence of a community, while abandoned programs are characterized by the departure of one.
Examples in the literature include the historical study of certain pre-modern technologies, the comparative grammar of language families with few living speakers, several questions in soil microbiology before its revival in the past two decades, and large portions of the history of women’s intellectual contributions before the development of feminist scholarship made the question legible.
3.2 Abandoned Research Programs
An abandoned research program is one that was active at an earlier period and was discontinued for reasons unrelated to its intellectual merits. The discontinuation may be traceable to a major funder’s shift in priorities, to the death or retirement of a founding figure, to a political climate that made the work professionally costly, to the rise of a competing paradigm that crowded the program out, or to simple bad luck in the form of a few negative results that became unduly authoritative.
The category is intellectually important because abandoned programs often contain accumulated knowledge — published papers, archived data, trained personnel — that can be recovered at substantially lower cost than building a research program from scratch. The history of psychedelic research after the regulatory clampdowns of the 1970s is a well-documented case: the program’s revival in the past two decades has been able to draw on a pre-existing literature whose findings, methods, and questions had been preserved even when active research was suspended. Similar cases exist in fields as varied as fermentation chemistry, classical breeding genetics, and several areas of clinical nutrition.
The recovery of abandoned programs is one of the most tractable applied projects available to neglect studies, because the work of identifying the program, evaluating its merits, and recommending revival can be done with conventional historical and bibliometric methods.
3.3 Methodologically Inaccessible Questions
Some questions cannot be productively studied without enabling tools that do not yet exist or have not yet been applied. These questions are not neglected in the ordinary sense — researchers may be perfectly aware of them and may be waiting for the methods to mature — but they constitute a distinct category because the conditions for their study are external to the question itself.
The category is interesting for neglect studies because methodological inaccessibility is itself often a product of attention patterns. Tools are developed where there is demand for them, and demand is shaped by which questions a research community considers important. A question that has been treated as unimportant for a generation will not generate demand for the tools needed to study it, and the absence of tools will then be cited as the reason the question remains unstudied. The cycle is self-sustaining and breakable only by deliberate intervention, often from outside the field in which the question sits.
Examples include large portions of the microbiome literature before sequencing costs dropped, the study of rare cognitive phenomena before reliable measurement instruments were developed, and several areas of historical climate research before the development of ice-core methods.
3.4 Interstitial Questions
Interstitial questions fall between established disciplines, in the spaces where no department has institutional responsibility and no journal has editorial scope. The interdisciplinarity literature has documented this problem extensively but has tended to treat it as a feature of certain individual scholars’ careers rather than as a systematic distortion of the research landscape.[^1]
The interstitial category is large and growing, in part because the problems that most exercise public policy — climate, public health, technology governance, mental health, demographic change — are characteristically multi-disciplinary, while the institutional apparatus of the academy remains organized around disciplines that were formalized a century ago. The mismatch is not absolute, since interdisciplinary centers and joint appointments exist, but it is substantial enough that many genuinely important questions sit in the seams between fields that each regard them as belonging primarily to the other.
The category includes questions in the philosophy of medicine that fall between philosophy departments and medical schools, questions in the political economy of science that fall between political science and science studies, and questions in the history of technology that fall between history departments and engineering schools.
3.5 Peripheral Inquiries
Peripheral inquiries are questions whose neglect is associated with the geographic, linguistic, or institutional location of the scholars best positioned to pursue them. A question pursued primarily by scholars in regions outside the dominant publication networks, or in languages other than the dominant scholarly languages, will receive systematically less attention than an equally important question pursued from a central location, even when the work itself is of comparable quality.
The category overlaps with broader concerns about epistemic inequality in the global knowledge system, which have been developed by scholars working under headings such as decolonial epistemology, global knowledge production, and Southern theory.[^2] Neglect studies has a more limited interest in these issues than those broader literatures: its concern is specifically with the patterns by which attention fails to reach particular questions, rather than with the wider normative arguments about whose knowledge counts. But the patterns overlap substantially, and neglect studies will need to draw on the broader literatures while maintaining its own focus.
Examples include the slow incorporation of indigenous ecological knowledge into mainstream ecology, the limited circulation of social-science scholarship from Latin America and Africa in the dominant English-language journals, and the asymmetry between the volume of work on northern-hemisphere ecosystems and the volume on southern-hemisphere ones.
3.6 Sensitive Questions
Sensitive questions are those whose pursuit imposes professional, political, or commercial costs on researchers. The costs may be direct — loss of funding, denial of tenure, harassment — or indirect — informal exclusion from networks, difficulty publishing, reputational damage. The mechanisms are well documented in the suppression-of-dissent literature[^3] and in the related literature on forbidden knowledge.[^4]
The category requires particular methodological care, because claims that a question is sensitive can be made for tactical reasons as well as for descriptive ones, and the field’s credibility depends on distinguishing genuine cases from rhetorical ones. A serious instance of sensitive neglect has several markers: documented cases of professional cost to researchers who pursued the question, evidence that the question is empirically tractable, evidence that the question is important on grounds that would be recognized by parties with different prior commitments, and evidence that the suppression mechanism operates across institutions rather than reflecting the judgment of a single funder or department.
Examples that have been studied in the literature include certain questions in the epidemiology of industrial exposures, certain questions in the social-science study of intelligence and behavior, and certain questions about the long-term effects of widely used pharmaceuticals. The field will need to handle such cases with particular discipline, because the political stakes are high and the temptation to use the field as a vehicle for advocacy in particular directions will be persistent.
3.7 Constituency-Less Questions
Constituency-less questions are those whose neglect is associated with the absence of any organized stakeholder community to advocate for their study. The priority-setting partnership literature has demonstrated that organized constituencies — patient groups, professional associations, advocacy organizations — can substantially shift research portfolios when they articulate research priorities clearly.[^5] The converse is that questions whose stakeholders are absent, diffuse, future, or non-human are systematically underserved.
The category includes questions whose affected parties are not yet born (most questions about long-term environmental change, demographic projection, and intergenerational policy), questions whose affected parties cannot articulate their concerns (questions about cognitive impairment, very young children, and several categories of animal welfare), questions whose affected parties are too dispersed to organize (many questions about everyday consumer products and low-grade environmental exposures), and questions whose affected parties exist but have not formed advocacy structures (many questions about rare conditions and small populations).
This category is particularly important for neglect studies because the priority-setting partnership model, which has been one of the most effective tools for redirecting research attention, by its construction cannot reach constituency-less questions. The field will need to develop methods for representing the interests of absent constituencies in priority discussions, while remaining honest about the difficulty of doing so without simply substituting the researcher’s preferences for the constituency’s.
4. Intellectual Antecedents
The preface introduced five literatures that constitute the most direct intellectual antecedents of neglect studies. This section develops the discussion of each and adds several smaller literatures that the preface did not have space to address. The aim is not a comprehensive review — that work belongs in a separate handbook — but a map of the conceptual resources the field can draw on and the gaps that remain when those resources have been assembled.
4.1 Agnotology
Agnotology, as named and developed by Robert Proctor and Londa Schiebinger in the 2008 collection that effectively founded the field,[^6] takes ignorance as a positive object of study rather than as the mere absence of knowledge. The field has produced powerful case studies, particularly Proctor’s own work on the tobacco industry’s manufacture of doubt about the health effects of smoking[^7] and Naomi Oreskes and Erik Conway’s parallel work on climate science.[^8] The field has also developed a useful conceptual vocabulary, distinguishing among ignorance as native state, ignorance as lost realm, and ignorance as strategic ploy — the third being the category that has received the most attention.
For neglect studies, agnotology is the most directly relevant antecedent, and the case for treating the new field as an expansion of agnotology rather than as a separate enterprise is serious. The case against is that agnotology’s center of gravity has settled firmly on strategic ignorance — the manufactured doubt produced by interested actors — while the larger and arguably more consequential category of passive neglect has received much less attention within the field. A neglect-studies enterprise that took agnotology’s core methods and applied them to the passive category would be a natural extension; whether the extension is best pursued under the agnotology banner or under a new name is a question of strategy more than of substance.
4.2 The Sociology of Undone Science
The undone-science literature, developed by David Hess, Scott Frickel, and their collaborators,[^9] approaches the same problem from a different direction. Where agnotology asks how ignorance is produced, the undone-science literature asks how civil-society actors identify research that institutional science declines to undertake. The empirical work has concentrated on environmental health, energy, and food systems, with notable studies of community concerns about industrial pollution that mainstream toxicology had not investigated.
For neglect studies, the contribution of the undone-science literature is methodological as much as substantive. The literature has developed careful procedures for documenting how research agendas are set, how civil-society actors challenge them, and how the resulting contestation reshapes the research landscape. Those procedures are directly applicable to neglect studies, with the qualification that the undone-science literature has confined itself to cases in which an organized constituency exists. The constituency-less category in the taxonomy above identifies the territory where the undone-science approach cannot reach without methodological extension.
4.3 Metascience
Metascience has emerged over the past two decades as a quantitative study of the research enterprise itself, with substantial institutional infrastructure including the Center for Open Science, the Meta-Research Innovation Center at Stanford, and a growing number of dedicated journals.[^10] The field’s central concerns have been research quality, reproducibility, and the demographic and institutional patterns of scientific careers.
For neglect studies, metascience is the closest existing methodological home and the most plausible institutional partner. Metascience already employs the bibliometric, scientometric, and computational methods that neglect studies will need, and several metascience research groups have begun work on research-coverage questions that overlap directly with the proposed field’s agenda. The argument for treating neglect studies as a subfield of metascience is therefore stronger than the argument for treating it as a subfield of agnotology. The argument against is that metascience’s institutional identity has formed around quality-and-reproducibility questions, and the coverage agenda has so far been peripheral within it. Whether that peripheral position is a stable foundation for the proposed field, or whether the coverage agenda needs its own institutional vehicle, is a strategic question that subsequent papers in this series will need to address.
4.4 Priority-Setting Research
The priority-setting research literature, exemplified by the James Lind Alliance methodology[^11] and the broader patient-and-public-involvement movement in health research,[^12] has developed structured procedures for eliciting research questions from affected communities and comparing them to existing research portfolios. The findings have been consistent across dozens of applications: substantial fractions of the questions that matter to patients, carers, and clinicians are not being addressed by ongoing research, and the magnitude of the mismatch is generally larger than researchers anticipate before the priority-setting exercise is conducted.
For neglect studies, the priority-setting literature offers a well-validated methodology that the field can adopt directly for one important category of cases — those in which an articulate constituency exists. The literature has been less developed for cases without organized constituencies, for foundational research questions, and for humanities scholarship, all of which the proposed field will need to address. Extensions of the priority-setting methodology to these cases are an open methodological problem and a candidate for early field-building work.
4.5 The Research-Waste Literature
The research-waste literature, associated with the REWARD initiative in The Lancet[^13] and with the broader work of Iain Chalmers, Paul Glasziou, and their collaborators, has documented that a substantial fraction of biomedical research effort is misallocated relative to the questions that matter to patients and clinicians. The estimates have been controversial in their specifics — the often-cited figure of eighty-five percent waste has been challenged — but the general finding is robust: research portfolios are not optimally allocated, and the gap between optimal and actual allocation is large enough to matter.
For neglect studies, the research-waste literature is a sibling enterprise rather than an antecedent in the strict sense. The two share a premise (the distribution of research effort is improvable) and differ in their focus (waste within active programs versus absence of programs at all). The relationship between them is roughly that the research-waste literature studies the misallocation of attention within the set of questions being asked, while neglect studies studies the misallocation of attention across the set of questions that could be asked. Both are needed, and a mature research-policy enterprise would treat them as complementary rather than competing.
4.6 History and Philosophy of Science
The history and philosophy of science have a long tradition of attention to questions that bear on neglect studies, even when the term has not been used. The historical literature on “lost sciences” — alchemy, phrenology, mesmerism, Lysenkoism — has implicitly addressed the question of how research programs end, sometimes legitimately and sometimes for reasons that look different in retrospect. The philosophical literature on theory choice, particularly in the post-Kuhn tradition, has addressed the question of how research communities allocate effort across alternative paradigms.[^14] The sociology of scientific knowledge has examined how methodological commitments shape what counts as a legitimate question.[^15]
For neglect studies, these literatures provide essential context and a stock of case studies, but they have not coalesced into a unified field with shared methods. The history of “lost sciences” has been particularly underdeveloped as a systematic enterprise, perhaps because the cases that historians most enjoy are those that turn out to have been correctly abandoned, while the cases of greatest interest to neglect studies are those that turn out to have been abandoned prematurely.
4.7 Library and Information Science
Library and information science has developed substantial bibliometric and scientometric infrastructure that is directly applicable to neglect studies. The discipline’s tools for mapping the structure of scholarly literatures — citation analysis, topic modeling, co-occurrence networks, coverage analysis — are the technical foundation on which large-scale neglect-mapping must rest.[^16]
For neglect studies, the relevant point is that the technical infrastructure already exists and is mature. What has been missing is a research agenda that uses it to ask coverage questions systematically. The mapping of negative space requires inverting the usual citation-analysis question — rather than asking which topics are most central, asking which topics are conspicuously absent given the structure of adjacent fields — and this inversion is a methodological extension rather than a wholly new technique.
4.8 Smaller Literatures
Several smaller literatures address pieces of the field’s territory and deserve mention. The literature on negative results and publication bias[^17] addresses the question of which findings within active research programs fail to enter the published record, which overlaps with neglect studies at the case level. The literature on the demographics of scientific careers[^18] addresses the question of which questions are pursued because of who is in a position to pursue them. The literature on funding-effects-on-research[^19] addresses the question of how grant structures shape research portfolios. The literature on academic freedom and self-censorship[^20] addresses the conditions under which researchers decline to pursue questions they would otherwise be interested in.
Each of these literatures contributes a piece. None of them, alone or together, constitutes the field that this series proposes to build.
5. Boundary Problems
Three boundary problems deserve explicit treatment, because the field’s coherence depends on handling them well.
The first is the boundary between neglect studies and ordinary disciplinary self-criticism. Every discipline has internal voices arguing that some of its questions are under-attended, and the work of those voices is healthy and necessary. Neglect studies is not in competition with disciplinary self-criticism; it is a meta-level enterprise that studies the patterns of attention across disciplines and the mechanisms that produce them. The relationship between the two is analogous to the relationship between economics and management studies: economics studies markets and firms in general, while management studies addresses the particular problems of running a particular firm. Both are legitimate, and neither replaces the other.
The second is the boundary between neglect studies and advocacy for particular neglected topics. Scholars who study a particular neglected topic and argue for more attention to it are doing important work, but they are not necessarily doing neglect studies. The distinction is roughly that the topic-specific advocate makes the case for their topic, while the neglect-studies scholar makes the case for a method of identifying which topics merit such cases. The two roles can be combined in a single scholar, but they should not be confused, and the field’s credibility will suffer if it is seen as a venue for any scholar to advance their preferred topic under a methodological banner.
The third is the boundary between neglect studies and political critique of the academy. Claims about what the academy neglects are sometimes made as part of broader political arguments about the academy’s commitments, biases, or institutional location. Those broader arguments are legitimate subjects of debate, but they are not the same as neglect studies, and the field will damage itself if it allows itself to be conscripted into them. The discipline required is to focus on empirically tractable questions about attention patterns and their mechanisms, while leaving the larger political questions to the venues in which they are appropriately conducted. The field will need to be hospitable to scholars whose underlying political commitments differ, because the patterns of neglect cut across the political spectrum and the field’s empirical credibility depends on demonstrating this in practice.
6. Conclusion
This paper has proposed a working definition of scholarly neglect, a taxonomy of seven overlapping categories, and a map of the intellectual antecedents on which the field can draw. The definition emphasizes that neglect studies is concerned with deficits in attention that are produced by mechanisms other than considered judgment, and that are large enough and the topics important enough to merit study. The taxonomy distinguishes orphan topics, abandoned research programs, methodologically inaccessible questions, interstitial questions, peripheral inquiries, sensitive questions, and constituency-less questions, with the understanding that real cases belong to several categories at once. The antecedent discussion has located the field in relation to agnotology, the sociology of undone science, metascience, priority-setting research, the research-waste literature, the history and philosophy of science, library and information science, and several smaller literatures that address pieces of the same problem.
What remains undone after this paper, and what Paper 2 will need to take up, is the methodological work that distinguishes rigorous identification of neglect from impressionistic claim-making. The categories above provide a vocabulary; the methods that would allow a scholar to defensibly assert that a particular case belongs to one of them are the next step. The credibility of the field as a whole depends on those methods being developed seriously, applied carefully, and held to standards that would survive scrutiny from scholars who are skeptical of the enterprise. The skepticism is itself a healthy condition for the field to develop under, since a field whose business is the rigorous identification of neglected questions cannot afford to be rigorously identified as a producer of unfounded claims.
Notes
[^1]: The interdisciplinarity literature has been growing for several decades and has its own internal debates about whether interstitial work is best supported through dedicated interdisciplinary institutions or through joint appointments within existing disciplinary structures. Jacobs and Frickel (2009) provide a critical assessment of the field’s claims; the National Academies (2005) report on facilitating interdisciplinary research is the most influential institutional document.
[^2]: The relevant literatures here include the global knowledge production scholarship developed by Raewyn Connell (2007), the decolonial epistemology literature associated with Boaventura de Sousa Santos (2014), and the science-studies work on geographical patterns in research, exemplified by the bibliometric studies summarized in Mongeon and Paul-Hus (2016) on database coverage biases.
[^3]: The suppression-of-dissent literature has been developed most extensively by Brian Martin and colleagues (Martin, 1999, 2014), with case studies across multiple disciplines.
[^4]: The forbidden-knowledge concept was developed by Joanna Kempner and colleagues (Kempner et al., 2011) and has been applied to questions in several fields, including stem-cell research, behavioral genetics, and certain areas of social science.
[^5]: The James Lind Alliance has published outcome studies of its priority-setting partnerships demonstrating substantial mismatches between patient-clinician priorities and existing research portfolios (Crowe et al., 2015).
[^6]: Proctor and Schiebinger (2008) is the founding text. Proctor’s own introductory chapter, “Agnotology: A Missing Term to Describe the Cultural Production of Ignorance (and Its Study),” is the most cited single statement of the field’s program.
[^7]: Proctor (2011) is the most developed treatment.
[^8]: Oreskes and Conway (2010) is the standard reference.
[^9]: Hess (2007) is the foundational monograph; Frickel et al. (2010) is the most cited article-length treatment.
[^10]: Ioannidis (2018) provides an overview of metascience as a field. The Center for Open Science and the Meta-Research Innovation Center at Stanford are the most visible institutional homes.
[^11]: Cowan and Oliver (2021) is the official methodology guidebook; the Alliance’s website maintains a list of completed partnerships with their identified research priorities.
[^12]: The broader patient-and-public-involvement literature is large; INVOLVE (the U.K. NIHR initiative) and the Patient-Centered Outcomes Research Institute in the U.S. are the most institutionally consolidated examples.
[^13]: The REWARD series in The Lancet began with Chalmers and Glasziou (2009) and developed through the multi-paper 2014 series initiated by Chalmers et al. (2014).
[^14]: Kuhn (1962/2012) remains the most influential single statement; the post-Kuhn literature on theory choice is large and includes Lakatos (1970), Laudan (1977), and many subsequent contributions.
[^15]: Bloor (1976) and the Edinburgh school’s broader output are the classic statements; subsequent work in science and technology studies has developed the program in many directions.
[^16]: The bibliometric and scientometric literature is vast. Mongeon and Paul-Hus (2016) on database coverage is particularly relevant to neglect studies because it documents the biases built into the standard data sources on which large-scale mapping must rely.
[^17]: The publication-bias literature begins with Rosenthal (1979) and has produced a substantial subsequent body of work, most recently focused on registered reports and pre-registration as corrective mechanisms.
[^18]: The demographics-of-science literature has documented patterns by gender, race, national origin, and institutional affiliation; Stephan (2012) provides an overview from the economics-of-science perspective.
[^19]: Azoulay and colleagues’ work on the effects of different funding structures on research productivity (Azoulay et al., 2011) is among the most cited; the broader literature is reviewed in Stephan (2012).
[^20]: The academic-freedom literature has both U.S. and international branches; recent contributions include Whittington (2018) and the various reports of organizations such as the American Association of University Professors.
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