# Science Productivity of Earth-Observation Data Policy: A Difference-in-Differences Study of Open-Data Release on Mission Citation Yield

**Candidate:** JPL_ASTRO_EARTH_09

**Program:** COLLEGIUM 1st Battalion

**North Star / JPL category:** Earth Science Missions

**Hall-of-Shoulders methodological anchors:** Douglass North (new institutional economics, the mechanism); Simon Kuznets (measurement discipline, the proxy stance); the Callaway and Sant'Anna staggered-adoption difference-in-differences apparatus (the estimator)

**Date:** 2026-06-15


## Abstract

The data that a nation gathers about its own planet are held in trust for those who will study it, and the terms on which that trust is honored, whether the data are offered freely or withheld behind cost and process, shape what science the public investment can return. NASA Earth-science missions differ in when, and whether, they made their data freely and openly available; some adopted free-and-open release early, some late, and some operated under restricted or fee-based access for extended periods. This dissertation asks whether the transition to free-and-open data release produced a measurable upward break in a mission's downstream scientific output, measured as the rate of peer-reviewed publications that use the mission's data and the rate of formal citations to the mission's datasets, relative to matched restricted-access missions. It frames open-data release as an institutional rule change in the sense of Douglass North: a change in the rules of access that lowers the transaction cost of obtaining and reusing mission data and should, if the framework holds, raise the volume of impersonal downstream use. It treats the citation and publication counts in the discipline of Simon Kuznets and the national-accounts tradition, as constructed proxies for the latent quantity of scientific productivity whose error structure and possible relabeling must be stated before inference.

The design is a matched, staggered-adoption difference-in-differences event study built around each mission's open-data-policy adoption date, with restricted-access missions matched to open-access missions on sensor class and mission age and estimated with the heterogeneity-robust Callaway and Sant'Anna group-time apparatus. The named data are NASA Astrophysics Data System and Web of Science publication and citation counts keyed to Earth missions, NASA Earthdata and Distributed Active Archive Center data-access logs, and a hand-coded register of mission open-data-policy adoption dates. The falsifiable contribution is a single hypothesis pair. H0: open-data adoption has no effect on downstream publication or dataset-citation yield. H1: open-data adoption produces a positive upward break in those yields relative to matched restricted-access missions. Support for H1 is read off the event-study path under a pre-registered decision rule that requires flat pre-adoption leads, positive post-adoption lags with a positive and statistically distinguishable aggregated effect, and survival of that effect under the Rambachan and Roth sensitivity analysis; a publication rise unaccompanied by any distribution rise is read, under the Kuznets discipline, as relabeling rather than new use and also falsifies. The contribution moves the open-data-advantage question from the self-selecting article level, where it is dominated by author choice and selection bias, to the policy-event mission level, the unit at which NASA and the Jet Propulsion Laboratory actually set data policy. This document presents the full design and a pre-registered analysis plan. Reported numerical results are labeled illustrative and design-stage; they have not been executed on the full assembled dataset, and the result tables are specified but, by design, unpopulated.


## Table of Contents

- Abstract
- List of Tables
- Chapter 1. Introduction
  - 1.0 Overview and central argument
  - 1.1 The problem in full
  - 1.2 Institutional and historical context
  - 1.3 The research questions stated explicitly
  - 1.4 Significance for NASA, JPL, and the named stakeholders
  - 1.5 Scope and delimitations
  - 1.6 Definitions of key terms
  - 1.7 The single falsifiable contribution stated as H0 and H1
  - 1.8 Roadmap of the dissertation
- Chapter 2. Theoretical Framework
  - 2.0 Overview: the conceptual claim and the gap it closes
  - 2.1 North and the institutional lens: open data as a rule change that lowers transaction cost
  - 2.2 Kuznets and the measurement lens: the outcome as a constructed proxy
  - 2.3 The integrated conceptual model the empirical work tests
  - 2.4 From framework to estimand: why the mechanism implies a dynamic event-study path within matched strata
  - 2.5 Summary of the framework and its forward commitments
- Chapter 3. Literature Review
  - 3.0 Overview: what the literature establishes and where it falls short
  - 3.1 The open-access citation advantage: the core finding, the counterweight, and the self-selection threat
  - 3.2 The open-data and dataset-reuse citation advantage
  - 3.3 Field, funding, and topic heterogeneity of the advantage
  - 3.4 Policy- and mandate-level evidence: what changes when openness is imposed
  - 3.5 The mission-level natural experiment: Landsat and Copernicus as program-level evidence
  - 3.6 Synthesis: the two gaps and the propositions that follow
- Chapter 4. Data and Measurement
  - 4.0 Overview: measurement as the foundation of inference
  - 4.1 Mission-linked publication and citation counts
  - 4.2 Data-access logs: Earthdata and the Distributed Active Archive Centers
  - 4.3 The hand-coded open-data-policy adoption register
  - 4.4 Operationalization: the measurement table
  - 4.5 The Kuznets proxy-error statement
  - 4.6 Data quality, validation against known values, and access and ethics
  - 4.7 Coverage and the five carried limitations
- Chapter 5. Research Design and Identification
  - 5.0 Overview: the estimator and the problem it solves
  - 5.1 The estimator, and why the naive alternative is rejected
  - 5.2 The specification, written out
  - 5.3 Identification: the assumptions argued formally
  - 5.4 Matching and balance: the comparison group constructed before the difference
  - 5.5 Threats to validity, each with its mitigation
  - 5.6 The robustness battery, specified in advance
  - 5.7 Power and the minimum detectable effect
  - 5.8 Pre-registration commitment and the computational plan
  - 5.9 Chapter synthesis: how the design advances the argument
- Chapter 6. Analysis Plan and Expected Results
  - 6.1 The estimation procedure as a fixed pipeline
  - 6.2 The fixed decision rule and falsification conditions
  - 6.3 Expected signs and the mechanism reasoning behind them
  - 6.4 Design of the illustrative simulation
  - 6.5 Event-study and coefficient-path interpretation conventions
  - 6.6 How this chapter advances the argument
- Chapter 7. Discussion
  - 7.0 Overview: both verdicts are informative
  - 7.1 Implications under both outcomes
  - 7.2 Theoretical contribution back to each anchor
  - 7.3 Policy and mission implications for NASA, JPL, and stakeholders
  - 7.4 Engagement with rival explanations
  - 7.5 External-validity statement
  - 7.6 Confidence statement
  - 7.7 Chapter synthesis: the interpretation pre-committed
- Chapter 8. Conclusion
  - 8.0 Overview: the contribution restated
  - 8.1 The contribution, and what stands even if H1 is not confirmed
  - 8.2 Limitations, stated honestly
  - 8.3 A concrete future-research program
  - 8.4 Closing: reproducibility as the principle under test
- References
  - Prospectus seed-number crosswalk
  - Full reference list (148 entries, author-sorted)
- Appendix A. Variable and data dictionary
- Appendix B. Open-data-policy adoption register, schema and coding protocol
- Appendix C. Bibliographic-linkage rule and the no-prior-affiliation filter
- Appendix D. Pre-registration record and result-table templates
- Appendix E. Illustrative-simulation parameters


## List of Tables

- Table 3.1. Representative open-access citation-advantage studies: design, finding, and limitation (Chapter 3)
- Table 3.2. Open-data, reuse, and data-citation-practice literature and its bearing on the design (Chapter 3)
- Table 3.3. Policy- and mandate-level evidence: how each begins, but does not complete, the move to identification (Chapter 3)
- Table 3.4. Program-level natural-experiment evidence and its identification limit (Chapter 3)
- Table 4.1. Construct-to-measurement mapping (Chapter 4)

No figures are included; result figures are specified but unpopulated by the design-stage guardrail and are described in Chapter 6 and Appendix D.


# Chapter 1: Introduction

## 1.0 Overview and central argument

A mission that observes the Earth is, in the end, an instrument of public service, and the stewardship of what it returns deserves to rest on measured benefit rather than on confident assertion. This dissertation argues that the scientific return on a NASA Earth-science mission's free-and-open data release is, at present, asserted rather than estimated, and that the staggered timing of open-data adoption across NASA Earth missions makes it possible to estimate that return with a credible identification strategy for the first time at the level of the mission. The chapter's thesis is therefore not a finding but a claim about the structure of a problem and the adequacy of a design to address it: open-data release is an institutional rule change in Douglass North's sense [\[85\]](#ref-85), one that lowers the transaction cost of obtaining and reusing a mission's data; that cost reduction should, if the institutional framework holds, raise the volume of impersonal downstream use, observable as peer-reviewed publications that use the mission's data and as formal citations to the mission's datasets; and a matched, staggered-adoption difference-in-differences event study, disciplined by the measurement caution of the Kuznets national-accounts tradition, is the design that can separate that policy effect from secular trends and mission-specific characteristics. The single falsifiable contribution that follows is the hypothesis pair H0 and H1, stated verbatim in Section 1.7 and tested under a pre-registered decision rule. The rest of this chapter develops, qualifies, and bounds the thesis: it states the problem in full, places it in its institutional and historical context, breaks out the research questions, establishes the significance for NASA and the Jet Propulsion Laboratory and their named decision stakeholders, fixes the scope and delimitations, defines the key terms, and lays out the roadmap. The numerical illustrations that appear later are labeled illustrative and design-stage throughout; this is a complete design and pre-registered analysis plan, not a report of executed results.

Because the question is one of policy evaluation rather than of system or data-service design, the chapters argue in prose, and the one place the link between the study's objective and the decision it informs is stated, in Section 1.4, is given in plain language. The work does not produce a systems or capability architecture, and it does not borrow that vocabulary.

## 1.1 The problem in full

### 1.1.1 The scientific return on open release is asserted, not measured

NASA invests in Earth-science missions to generate knowledge about the Earth system. The investment is large, recurring, and justified by the downstream science the data enable. Yet the scientific return on that investment is realized only at the end of a chain that runs from the spacecraft and its instrument, through the ground system and the archive, to a researcher who obtains the data, analyzes them, publishes a finding, and is in turn built upon by others. Data-access policy sits squarely on that chain. A mission whose data are free, openly licensed, documented, and easy to obtain imposes a low cost on a prospective user. A mission whose data are restricted, fee-based, or encumbered by registration, eligibility review, and license negotiation imposes a higher cost. The question this dissertation addresses is whether lowering that cost actually raises the downstream scientific yield of a mission, and by how much.

The current state of practice answers that question by assertion. NASA's Science Mission Directorate has moved deliberately and publicly toward free-and-open release, and it now reports annual metrics on the publications, data, and software associated with its funded research. The directorate's policy presumes a mechanism: that open release increases use, and that increased use increases scientific output. The presumption is reasonable and widely shared, but at the level of the mission it is not an estimate. It is a stated expectation supported by program-level episodes and by an article-level literature whose unit of analysis is not the mission. The gap between what is asserted and what is measured is the problem this dissertation exists to close.

### 1.1.2 What a mission-level, identified estimate located in event time would provide
The desired state is a mission-level, identified estimate of the publication and dataset-citation yield of open release, located in event time and decomposed by sensor class, that lets the cost of open-release infrastructure be weighed against a measured benefit rather than an asserted one. Building and operating a Distributed Active Archive Center, curating data products to a reusable standard, and maintaining access tooling are not free. A defensible estimate of the downstream scientific yield of open release lets those costs be set against a measured return, lets the response be located in time so that recent policy changes can be evaluated before their full effect has materialized, and lets the design of future missions in the Earth Science portfolio make the open-data decision at formulation rather than retrofitting it after launch.

### 1.1.3 The mission is the funded unit, but the evidence is at the article level

The gap between the current and desired states has a precise shape. There is a large and careful literature on the open-access citation advantage for journal articles and a smaller literature on the open-data citation advantage for datasets, surveyed in Chapter 3. Almost all of that work takes the individual article or the individual dataset as its unit of analysis. The unit that NASA and JPL actually fund and operate is the mission, and the policy lever that NASA actually pulls is mission-level or directorate-level data policy. Little quantitative work treats the mission as the unit of analysis and the mission's open-data adoption as the treatment. The point is bounded and specific: the gap is not that openness has never been studied, but that it has not been studied at the unit at which the policy decision is made. The literature's own framing sits overwhelmingly at the article and dataset level [\[19\]](#ref-19), [\[32\]](#ref-32), [\[34\]](#ref-34), [\[63\]](#ref-63), [\[75\]](#ref-75), [\[96\]](#ref-96)], and a policy estimate is only directly usable for a decision when its unit matches the unit of the decision. Program-level episodes such as Landsat [\[122\]](#ref-122), [\[132\]](#ref-132)] are closer to the mission unit and serve as the design precedent rather than a counterexample. The one finding that would defeat the point, a prior mission-level staggered-adoption study of NASA data policy, is one this dissertation has searched for and not found, which is why the contribution is framed as filling a gap rather than refining an existing estimate.

### 1.1.4 Consequence of inaction

The consequence of leaving the gap open is that NASA and JPL keep making recurring data-release and data-system-investment decisions against an asserted benefit. A directorate-level policy is credited or discredited on the strength of episodes and anecdote. The binding constraint on a mission's scientific yield, which could be access cost, or analysis funding, or data-product maturity, or the size of the relevant research community, is never separated, so the agency cannot tell whether further investment in open-release infrastructure is the highest-return use of a marginal dollar or whether that dollar would do more for science spent on funding analysis or maturing products. This is the consequence the design is built to avert, and it explains why a null result, far from being a disappointment, is informative: a credible failure to reject the null would redirect attention to the constraints that actually bind.

## 1.2 Institutional and historical context

### 1.2.1 The institutional move toward free-and-open release

The problem is situated in a definite institutional history. The United States has debated and revised its policy for Earth observation from space for decades; the question of who may obtain government remote-sensing data, on what terms, and at what price is an old one, and the early policy posture was considerably more restrictive than the current one [\[138\]](#ref-138)]. Over time, and unevenly across missions and data systems, the posture shifted toward openness. NASA's Earth Science Data Systems program developed an architecture of open data, services, and software [\[147\]](#ref-147)], built and sustained the Distributed Active Archive Centers as long-term active archives with an explicit stewardship mandate [\[145\]](#ref-145)], and the agency articulated a Plan for Increasing Access to the Results of Scientific Research and, more recently, a Science Mission Directorate Scientific Information Policy with annual implementation metrics. The trajectory is one of an institution lowering, in stages and across missions, the cost a prospective user faces in obtaining and reusing mission data. That trajectory is the empirical substrate of this study: because the move to openness happened at different times for different missions, the timing is staggered, and staggered timing is what a modern difference-in-differences design needs.

### 1.2.2 The Landsat precedent as the design template

The single most important historical episode for this dissertation is the Landsat program's transition to a free-and-open data policy in 2008. The episode is unusually well documented, and the documentation is consistent in its qualitative finding. Wulder and colleagues report that the policy change was followed by a rise in scene distribution from tens of thousands to tens of millions of scenes per year and by a sharp expansion in publications and operational products [\[122\]](#ref-122). Zhu and colleagues corroborate the program-level effect and quantify several of its dimensions [\[132\]](#ref-132). The fifty-year retrospective on Landsat science and impacts places the open-data switch within a longer arc of the program's scientific influence and treats the policy change as a turning point in the program's usage and output [\[77\]](#ref-77). The downstream consequences reach beyond bibliometrics: free and open access to satellite data has been argued to be a precondition for entire domains of application, including biodiversity conservation, where the cost of data once foreclosed the large-area, repeated analyses that conservation monitoring requires [\[121\]](#ref-121). A grey-literature synthesis on how the Landsat open-data policy advanced understanding of environmental change collects the qualitative case in one place [\[135\]](#ref-135)].

The Landsat episode demonstrates that mission-level open-data policy can be associated with a large change in usage and output. It does not, by itself, identify a causal effect, and the reason it does not is the methodological hinge of this entire dissertation. Landsat is a single mission observed before and after a single date, with no contemporaneous control. Any number of things changed in remote sensing between the years before and the years after 2008, and a single before-and-after comparison cannot separate the policy from the secular trend, from the maturation of the program, or from coincident changes in computing, in data systems, or in the size of the user community. The proposition that the Landsat switch raised scientific output is, at the level of evidence, an association observed in one unit over time. That association is strong and well documented [\[77\]](#ref-77), [\[122\]](#ref-122), [\[132\]](#ref-132)]; what would turn it into a causal estimate, namely a credible counterfactual for what Landsat's output would have been absent the policy, is exactly what a single uncontrolled before-after comparison cannot supply. The association is nonetheless suggestive and motivates the design, and the standard objection to any single interrupted time series applies here, that a coincident shock could account for the break. The contribution of this dissertation, stated in one line, is to embed the Landsat-type episode in a multi-mission, matched, staggered-adoption design that supplies the missing contemporaneous control and can therefore separate the policy effect from the secular trend.

### 1.2.3 The contemporary policy frame in which the question now sits

The question is also live in a contemporary frame. Reviews of satellite remote-sensing data policy continue to argue, from the accumulated record, that free and open data carry first-order benefits [\[90\]](#ref-90), and the application literature continues to demonstrate the breadth of downstream use that open Earth-observation data enable, from coastal-erosion and shoreline monitoring [\[23\]](#ref-23) to the pursuit of the Sustainable Development Goals [\[131\]](#ref-131). The Copernicus program in Europe offers a second, partially independent natural experiment in user uptake following an open-data posture, with its own documented trajectory from data to applications [\[68\]](#ref-68). These contemporary cases are not the object of estimation here, which is confined to NASA Earth-science missions, but they establish that the mechanism the study tests is neither historically peculiar to Landsat nor confined to a single agency, and they sharpen the policy stakes: the directorate-level Scientific Information Policy is a current commitment whose mission-level mechanism this dissertation is designed to test.

## 1.3 The research questions stated explicitly

The dissertation is organized around one principal research question and a small set of subordinate questions that the design must answer in order to answer the principal one. They are stated here explicitly so that the reader can hold them against the design in Chapters 4 through 6.

**Principal research question.** For NASA Earth-science missions, does the transition to free-and-open data release produce a measurable upward break in a mission's downstream scientific output, measured as the rate of peer-reviewed publications that use the mission's data and the rate of formal citations to the mission's datasets, relative to matched restricted-access missions?

**Subordinate question 1, on the mechanism's ordering.** If an effect exists, does it appear first in distribution and download volume and only later in publications, as the institutional access-cost mechanism predicts, or does a publication change appear without any accompanying distribution change, which would point to a counting or attribution change rather than to genuinely new use? This question is what makes the Earthdata and Distributed Active Archive Center distribution logs an integral part of the design rather than a convenience.

**Subordinate question 2, on dynamics.** If an effect exists, is it immediate or gradual? North's account of path dependence predicts a gradual adjustment, because user communities that formed under restricted access carry workflows, intermediaries, and expectations that persist after the rule changes. This question is what requires a dynamic event-study path indexed by event time rather than a single before-after difference.

**Subordinate question 3, on heterogeneity.** If an effect exists, is it uniform across mission types, or does it vary by sensor class? The Landsat evidence is concentrated in optical imaging, and the size of the latent user community plausibly differs across optical, radar, microwave, lidar, and spectrometer missions. This question is what requires the effect to be estimated and reported by sensor class rather than averaged into a single number.

**Subordinate question 4, on identification.** Can the effect be identified at all, given that missions may adopt open release precisely when their output is already rising? This is the question of parallel trends, and it is logically prior to the others: if the pre-adoption leads are positive and trending, the design does not identify the effect and no causal claim is made regardless of what the post-adoption coefficients show. This question is what makes the lead test and the sensitivity analysis the first things examined, not the last.

These questions are not independent inquiries to be answered in sequence; they are the components of a single estimand, and the answer to the principal question is read off the same event-study path that answers the subordinate ones. The decision rule in Section 1.7 and in Chapter 6 fixes how that reading is done.

## 1.4 Significance for NASA, JPL, and the named stakeholders

### 1.4.1 The decision the estimate informs

The significance of the study is best stated as the decision it informs, in plain language and without the vocabulary of enterprise architecture, which would be misapplied here. The strategic objective is to maximize the scientific return on the agency's investment in Earth-science missions. The recurring decision that bears on that objective, and that this dissertation is built to inform, is whether and when to fund open-data release and the supporting data-system infrastructure, made ideally at mission formulation rather than retrofitted after launch. The link between the objective and the decision runs through exactly the quantity the study estimates: the downstream scientific yield of open release. An estimate of that yield, located in event time and decomposed by sensor class, converts the open-data decision from one made against an asserted benefit into one made against a measured one. That is the whole of the objective-to-decision link, stated plainly; the study does not model a capability, a system function, or a data-service exchange, and it does not borrow that vocabulary.

### 1.4.2 Who uses the estimate
The estimate matters to several identifiable classes of decision-maker. The Science Mission Directorate sets and revises data policy at the directorate level; a mission-level estimate of the mechanism that policy is intended to activate is the kind of evidence that lets a directorate-level commitment rest on more than episode and assertion. The program offices and mission formulation teams that decide, mission by mission, how data will be released and how much to invest in the systems that support release are the proximate users of an estimate located at the mission unit. The Distributed Active Archive Centers and the Earth Science Data Systems program, which bear the recurring cost of curation, archiving, and access tooling [\[145\]](#ref-145), [\[147\]](#ref-147)], have a direct interest in whether that cost can be set against a measured return. The Jet Propulsion Laboratory, as an operator of Earth-observation missions and as an institution that makes recurring data-release and data-system-investment choices, is a named stakeholder in the same sense: the estimate speaks to choices it actually makes. What gives the estimate this standing is the documented existence of these decision processes and their recurring data-policy content. An estimate at the unit of a decision is usable by the maker of that decision in a way that an estimate at a different unit is not. The estimate is internal to NASA Earth-science missions in the observation window, and its transfer to other agencies or to future missions in a changed publishing environment is a matter of external validity argued in Chapter 7, not assumed here.

### 1.4.3 Why a null is significant too

The study is significant under both outcomes, and this symmetry is a deliberate feature of the design rather than a rhetorical hedge. If the transition to open release produces a measurable upward break, the study converts an asserted benefit into a measured one and locates it in time. If, once confounders are controlled, the transition produces no measurable break, the study has shown that access cost is not the binding constraint on a mission's scientific yield within this sample. That finding is itself actionable: it redirects attention, and by implication marginal investment, toward the constraints that do bind, whether analysis funding, product maturity, or community size. A design that can only confirm the policy it examines is of limited value to a decision-maker; a design that can falsify it is worth more. The decision rule is built so that both outcomes are reportable and neither is foreclosed by the specification.

## 1.5 Scope and delimitations

The scope of the study is bounded deliberately, and the boundaries are stated here so that no claim in the dissertation is read as reaching beyond them.

**Population.** The study covers NASA Earth-science missions for which a clear access regime and an open-data adoption date can be coded and for which bibliographic linkage to a mission is feasible. It does not cover NASA astrophysics, heliophysics, or planetary missions, whose data systems, user communities, and citation norms differ; it does not cover non-NASA missions except where the Copernicus and Landsat episodes serve as design precedents or external-validity touchstones; and it does not cover commercial Earth-observation data, whose access economics are different in kind.

**Cardinality.** The number of distinct NASA Earth-science missions with codable access regimes is modest, on the order of tens rather than hundreds. This is a first-order delimitation with consequences that run through the entire design. The study is more exposed to small-sample inference problems than an article-level study of half a million records [\[19\]](#ref-19), the matching pool for some sensor classes may be thin, and the dataset-citation arm, restricted further to a recent window because formal data citation is sparse early, will have limited statistical power. These consequences are not hidden. They shape the choice of estimator, the use of wild-cluster bootstrap inference, and the explicit power caveats carried through Chapters 5 and 6.

**Temporal window.** The study observes missions over the window for which the bibliographic, distribution-log, and policy-register data can be assembled and linked. The window is bounded below by the availability of indexed publication and citation data and the codability of access regimes, and above by the data cutoff. Recent adoptions whose full effect has not yet had time to materialize are observed only over their available post-adoption periods, which is one reason the response is estimated as a dynamic path rather than a single long-run difference.

**Outcome scope.** The study measures three outcomes: the mission-linked peer-reviewed publication rate, the formal dataset-citation rate, and the distribution or download volume. It does not measure scientific quality, societal impact, or economic value directly; those lie outside the bibliometric and log-based measures the study can construct, and the relationship between citation counts and any of them is the kind of proxy relationship the Kuznets discipline in Section 1.6 and Chapter 2 requires be stated rather than assumed.

**What the study does not claim.** The study does not claim to estimate the effect of open access on individual articles, which is the existing literature's domain; it does not claim a uniform effect across mission types, which its own heterogeneity estimates are designed to test rather than presuppose; and it does not, at this stage, report any executed result. Every numerical value in the document is illustrative and design-stage, included to fix the form of the expected output and the operation of the decision rule, not to report a finding.

## 1.6 Definitions of key terms

The argument depends on a small set of terms whose precise meaning is fixed here and carried, without drift, through every subsequent chapter. Where a term has a technical definition in the shared design bible, that definition is reproduced exactly.

**Free-and-open data release.** The release of a mission's data without fee, under an open license, with the data findable through persistent identifiers and obtainable without registration, eligibility review, or approval beyond what is required to operate the access system. The definition is functional rather than nominal. A policy that is open in license but practically inaccessible because of missing tooling or undocumented products has not lowered the relevant transaction cost and is not coded as free-and-open release. The vocabulary that operationalizes the distinction between nominal and functional openness is the FAIR vocabulary of findability, accessibility, interoperability, and reusability [\[120\]](#ref-120); a mission coded as open but functionally encumbered is reclassified in a robustness check.

**Restricted access.** Any access regime that imposes a cost on a prospective user beyond the functional cost of obtaining an openly released file: a fee, a registration or eligibility requirement, a license negotiation, an approval step, or a practical encumbrance such as missing documentation or tooling that raises the cost of reuse. Restricted-access missions, matched to open-access missions, supply the comparison information in the design.

**Mission-period.** The unit of analysis. Each NASA Earth-science mission is observed over a sequence of periods, with periods defined as years and, in a robustness specification, as quarters. The panel is unbalanced because missions enter and exit the observation window at different times and because some missions never adopt open release within the window. The treatment is the open-data-policy adoption event; treated missions adopt at different periods, and never-adopters and not-yet-adopters supply comparison information.

**Treatment.** The open-data-policy adoption event. A mission is treated from the period of its transition to free-and-open release, coded from the hand-coded adoption-date register described in Chapter 4. Adoption timing is staggered across missions.

**Publication rate (Outcome 1).** The count, per mission-period, of peer-reviewed articles that use the mission's data, identified by a combination of mission and instrument name matching, dataset-identifier matching, and acknowledgment-text matching, with the matching rule held fixed across the pre- and post-adoption periods so that a change in counting practice cannot masquerade as a change in output. A supplementary specification restricts to articles by authors with no prior affiliation to the mission team.

**Dataset-citation rate (Outcome 2).** The count, per mission-period, of formal citations to the mission's datasets as first-class objects, in the sense of the Data Citation Principles [\[27\]](#ref-27) and the repository roadmap [\[33\]](#ref-33). Because formal data citation became common only recently, this outcome is treated as available for the later part of the window and is analyzed separately rather than pooled with publication counts.

**Distribution volume (Outcome 3).** Access and download events recorded in Earthdata and Distributed Active Archive Center logs, per mission-period, used as an early-response outcome and as an independent mechanism check on whether a publication change is accompanied by a genuine change in use.

**Impersonal use.** Downstream use of a mission's data by researchers who were not part of the mission team. The term is North's: the prediction that lowering access cost raises the volume of impersonal exchange is the mechanism the study tests, and the no-prior-affiliation specification operationalizes impersonal use directly so that the effect is not an artifact of the mission team citing its own data more readily once citation became easy.

**Proxy.** A constructed, measurable indicator that stands in for a latent quantity it is not. A citation count is a proxy for scientific productivity, not the productivity itself; the Kuznets discipline, developed in Chapter 2, requires that the proxy's error structure be stated, namely that citation counts are right-skewed, accumulate with a lag, depend on field size and citation norms, and are sensitive to the indexing coverage of the source database [\[41\]](#ref-41), [\[62\]](#ref-62), [\[76\]](#ref-76)].

## 1.7 The single falsifiable contribution stated as H0 and H1

The dissertation makes one falsifiable claim, stated as a hypothesis pair on the mission as the unit of analysis. The statements are reproduced verbatim from the approved design and are carried, unaltered, into the analysis plan and the decision rule.

**H0 (null):** The transition to free-and-open data release has no effect on a mission's downstream peer-reviewed publication rate or its dataset-citation rate, relative to matched restricted-access missions.

**H1 (alternative):** The transition to free-and-open data release produces a measurable upward break, an increase in level or slope, in a mission's downstream peer-reviewed publication rate and dataset-citation rate, relative to matched restricted-access missions, in the periods after adoption.
The claim is falsifiable in both directions, and the conditions are fixed before any estimation. The design produces a dynamic event-study path of coefficients indexed by event time, the periods since adoption, with the last pre-adoption period normalized to zero. Support for H1 requires three conditions jointly. First, the pre-adoption leads must be flat, that is, jointly indistinguishable from zero, so that no pre-trend is detectable. Second, the post-adoption lags must be positive and the aggregated overall effect positive and statistically distinguishable from zero. Third, the positive effect must survive the Rambachan and Roth sensitivity analysis [\[97\]](#ref-97) at the stated breakdown threshold, so that the result is reported as a robustness region rather than a single point. Failure to reject H0 occurs if the aggregated overall effect is not statistically distinguishable from zero or does not survive the sensitivity analysis; either outcome falsifies the contribution as stated. Two specific falsifiers deserve naming here, because each can halt the causal interpretation before the headline coefficient is read. The first is identification: if the pre-adoption leads are themselves positive and trending, the parallel-trends assumption is violated, the design does not identify the effect, and no causal claim is made regardless of the sign of the lags. The second is the Kuznets relabeling check: a publication rise unaccompanied by any distribution rise is read, under the measurement discipline, as a change in counting or attribution rather than as new use, and also falsifies the contribution.

This is the whole of the falsifiable contribution. It is one pair of hypotheses, tested under one pre-registered rule, and it is the thread to which every chapter of the dissertation attaches. The contribution is worth stating because of the documented association between openness and downstream use [\[19\]](#ref-19), [\[75\]](#ref-75), [\[77\]](#ref-77), [\[96\]](#ref-96), [\[122\]](#ref-122), [\[132\]](#ref-132)] together with the documented order-of-magnitude usage change after the Landsat switch [\[122\]](#ref-122), [\[132\]](#ref-132)]; what turns the motivating association into an identified estimate is the matched, staggered, heterogeneity-robust event study developed in Chapters 5 and 6; the estimate, if obtained, is conditional, design-stage, and internal to the population and window in Section 1.5; and what would defeat the contribution is any of the falsifiers just named, each checked explicitly and each sufficient on its own to overturn H1. Confidence in the contribution at this stage is therefore moderate and conditional at best: the design is complete and the identification strategy is credible, but no coefficient has been estimated, and the strength of any eventual claim will be bounded by the weakest of the stated limitations rather than the strongest part of the design.

## 1.8 Roadmap of the dissertation

The dissertation proceeds in eight chapters and a back matter, organized so that each chapter discharges one part of the argument and hands a fixed set of definitions and commitments to the next.

**Chapter 2, the theoretical framework,** develops the two methodological anchors that discipline the design. It builds North's institutional lens, in which open-data release is a rule change that lowers the transaction cost of impersonal exchange and should therefore raise impersonal downstream use, with a path-dependent and gradual response, and it imports the FAIR vocabulary to separate nominal from functional openness [\[85\]](#ref-85), [\[120\]](#ref-120)]. It then builds the Kuznets measurement lens, in which the citation and publication counts are constructed proxies with a stated, biased error structure, using the night-lights proxy literature [\[41\]](#ref-41), the national-accounts measurement literature [\[62\]](#ref-62), and the within-versus-reallocation distinction [\[76\]](#ref-76) to insist that a rise in the proxy be shown to be real new output before it is read as productivity. The chapter closes by assembling the two lenses into the conceptual model the empirical work tests and by showing why that model implies a dynamic event-study path within matched strata rather than a single before-after difference.

**Chapter 3, the literature review,** is the longest chapter and situates the contribution in the empirical evidence base. It reviews the open-access citation advantage and its systematic-review counterweight [\[32\]](#ref-32), [\[34\]](#ref-34), [\[63\]](#ref-63), [\[75\]](#ref-75), [\[96\]](#ref-96)], the open-data and dataset-reuse citation advantage and the data-citation-practice literature [\[19\]](#ref-19), [\[27\]](#ref-27), [\[33\]](#ref-33)], the field, funding, and topic heterogeneity of the advantage, the policy- and mandate-level evidence on what changes when openness is imposed rather than chosen, and the mission-level remote-sensing episodes of Landsat and Copernicus as program-level natural experiments [\[68\]](#ref-68), [\[77\]](#ref-77), [\[122\]](#ref-122), [\[132\]](#ref-132)]. It closes by stating the two gaps, that the evidence is article-level not mission-level and associational not identified, and the propositions that follow.

**Chapter 4, data and measurement,** describes each named data source in depth: the NASA Astrophysics Data System and Web of Science as a dual bibliographic source whose redundancy is a construct-validity defense against single-database indexing artifacts [\[60\]](#ref-60), the Earthdata and Distributed Active Archive Center distribution logs as an upstream usage measure and mechanism check, and the hand-coded open-data-policy adoption register with its double-entry, adjudication, and phased-transition handling. It provides the full operationalization table for the three outcomes and every covariate, states the Kuznets proxy-error structure explicitly, validates the measures against known values such as the documented Landsat distribution series, and carries the five stated limitations forward, each tied to a mitigation in the design.

**Chapter 5, the research design,** sets out the empirical strategy in full. It justifies the Callaway and Sant'Anna group-time average-treatment-effect estimator and shows, through the Goodman-Bacon decomposition, why the naive two-way fixed-effects estimator is unreliable under staggered timing and heterogeneous effects [\[14\]](#ref-14), [\[35\]](#ref-35)]. It writes out the dynamic event-study specification, argues the conditional parallel-trends identification within matched sensor-class-by-age strata, sets out the matching and balance machinery [\[8\]](#ref-8), [\[99\]](#ref-99), [\[111\]](#ref-111)], treats every threat to validity with its mitigation, specifies the robustness battery in advance [\[10\]](#ref-10), [\[30\]](#ref-30), [\[113\]](#ref-113)], and conducts the power analysis given a cohort of tens of missions.

**Chapter 6, the analysis plan,** is the design-stage heart of the dissertation. It states the estimation procedure as a numbered pipeline, fixes the decision rule and falsification conditions verbatim, lays out the expected signs with detailed mechanism reasoning per outcome, and presents the illustrative-simulation design that demonstrates the event-study path's shape and the decision rule's operation on synthetic data. Every number in the chapter is labeled expected or illustrative, and the result tables are specified but unpopulated by design: column headers, event-time rows, and the sensitivity-region template are laid out with the cells empty.

**Chapter 7, the discussion,** works through the implications under both outcomes, returns the result to each anchor to say what it would mean for North's access-cost mechanism and for the Kuznets proxy-versus-productivity distinction, states the policy and mission implications for NASA, JPL, and the named stakeholders with the plain-language objective-to-decision link, engages each rival explanation with its design defense, states sensor-class heterogeneity as the honest boundary of generalization, and gives an explicit, conditional, moderate-confidence reading of what the design can and cannot support.

**Chapter 8, the conclusion,** restates the contribution and what stands even if H1 is not confirmed, namely the mission-level design, the frozen-rule measurement discipline, and the assembled adoption register as contributions regardless of the sign of the effect; it states the limitations honestly; it lays out a concrete future-research program of assembling the panel and executing the Chapter 6 pipeline; and it closes on reproducibility as itself an application of the open-data principle the study examines.

The **back matter** compiles the full reference list, the variable and data dictionary, the adoption-register schema and coding protocol, the bibliographic-linkage rule and the no-prior-affiliation filter, the pre-registration document with the unpopulated result-table templates, and the illustrative-simulation code and parameters.

A single argumentative thread runs through all eight chapters. The question matters because data-access policy sits on the causal path between a mission and its scientific return, and openness is repeatedly associated with more downstream use [\[19\]](#ref-19), [\[75\]](#ref-75), [\[77\]](#ref-77), [\[96\]](#ref-96), [\[122\]](#ref-122), [\[132\]](#ref-132)], and the stakes are not small: the Landsat switch was followed by an order-of-magnitude rise in distribution and a sharp expansion in publications and operational products [\[77\]](#ref-77), [\[121\]](#ref-121), [\[122\]](#ref-122), [\[132\]](#ref-132)]. The design meets that question at the level of the causal mechanism rather than mere correlation, because a matched, staggered event study isolates the policy event from secular trends and mission characteristics and uses distribution logs as an independent upstream check [\[14\]](#ref-14), [\[35\]](#ref-35), [\[85\]](#ref-85)]. It earns its place over the simpler options because the naive estimator is biased under staggered heterogeneous effects, the article-level association cannot remove author self-selection, and the single-mission before-after has no contemporaneous control [\[35\]](#ref-35), [\[63\]](#ref-63)]. What it cannot rule out is held within bounds: the result is stated as conditional and design-stage, the proxy's biases are stated, the counting rule is frozen, pre-trends are tested, and the effect is reported as a robustness region [\[10\]](#ref-10), [\[62\]](#ref-62), [\[97\]](#ref-97)]. The introduction names these commitments so that the reader can hold each subsequent chapter against the part of the argument it is meant to carry.


# Chapter 2: Theoretical Framework

## 2.0 Overview: the conceptual claim and the gap it closes

This chapter advances a single claim: the downstream scientific yield of a free-and-open Earth-observation data policy is best understood as the equilibrium response of a population of prospective users to an institutional rule change that lowers the transaction cost of obtaining and reusing mission data, and the rise in any bibliometric indicator of that response must be shown to be real new use rather than improved counting before it can be read as a gain in scientific productivity. Two methodological anchors generate that claim and discipline it. Douglass North supplies the mechanism: institutions are the humanly devised rules of the game, an open-data policy is one such rule, and lowering the cost of impersonal exchange should raise its volume [\[85\]](#ref-85). Simon Kuznets, through the national-accounts tradition he founded, supplies the measurement stance: every aggregate is a constructed proxy with a stated and biased error structure, and a movement in the proxy is not yet a movement in the latent quantity it stands for [\[62\]](#ref-62). The conceptual model the empirical chapters will test is the conjunction of the two: a causal chain from rule change to falling access cost to rising distribution to rising impersonal publication to rising formal dataset citation, instrumented through proxies whose error structure is named in advance, and estimated as a dynamic path rather than a single before-and-after contrast.

The problem this chapter addresses is the distance between a strong intuition and a defensible inference. The prevailing understanding is that open release "obviously" helps, supported by a large article-level open-access citation-advantage literature [\[19\]](#ref-19), [\[32\]](#ref-32), [\[34\]](#ref-34), [\[75\]](#ref-75), [\[96\]](#ref-96)] and by a vivid single-mission episode in which the 2008 free-and-open Landsat policy was followed by an order-of-magnitude rise in scene distribution and a sharp expansion in publications [\[122\]](#ref-122), [\[132\]](#ref-132)]. What that intuition lacks is a framework precise enough to say what exactly is supposed to rise, through what mechanism, on what timescale, and what would count as evidence that the apparent rise is an artifact rather than a real effect. The intuition does not, by itself, distinguish a genuine increase in scientific use from a relabeling of pre-existing use, does not specify whether the response should be immediate or gradual, and does not tell the analyst which threats to construct validity must be closed before a coefficient is interpreted. Without that precision, NASA and the Jet Propulsion Laboratory continue to weigh the real and recurring cost of open-release infrastructure (Distributed Active Archive Center operation, product curation, access tooling) against a benefit that is asserted rather than theorized, and a finding of "more citations after open release" cannot be told apart from "the same work, now easier to count." This chapter answers that need by building the mechanism and the measurement discipline separately, then fusing them into the conceptual model and bridging from that model to the estimand.

The chapter proceeds in four substantive sections. Section 2.1 develops North's institutional framework, its primary source, and its transfer to the open-data problem, including the construct-validity discipline of separating nominal from functional openness through the FAIR vocabulary. Section 2.2 develops the Kuznets measurement lens through the applied national-accounts and satellite-proxy literature, establishing the proxy stance and the real-output-versus-relabeling distinction. Section 2.3 fuses the two into the integrated conceptual model the empirical work tests, with the proxy error structure made explicit at each node. Section 2.4 bridges from the conceptual model to the estimand, showing why the mechanism implies a dynamic event-study path within matched strata rather than a pooled before-and-after difference. Throughout, each causal claim is tied to a named mechanism rather than a bare correlation, and the confidence attached to it is calibrated to the design-stage evidence grade. No empirical result is reported; this is a conceptual chapter, and any illustrative magnitude is labeled as such.

## 2.1 North and the institutional lens: open data as a rule change that lowers transaction cost

### 2.1.1 The framework and its primary source

The first anchor is Douglass North's account of institutions as the rules of the game in a society, set out in *Institutions, Institutional Change and Economic Performance* [\[85\]](#ref-85). North defines institutions not as organizations but as constraints: "the humanly devised constraints that shape human interaction." Those constraints, formal and informal, exist because exchange is costly. His deeper claim, inherited from the transaction-cost tradition of Coase and developed into a theory of long-run economic change, is that the costliness of exchange has two components institutions act upon. The first is the cost of measuring the valuable attributes of what is being exchanged. The second is the cost of enforcing agreements about it. When exchange is personal, conducted repeatedly among parties who know one another, both costs are low because reputation and repeated dealing substitute for formal measurement and enforcement. When exchange becomes impersonal, conducted at distance among strangers who transact once, both costs rise sharply, and the gains from specialization and division of labor cannot be realized unless institutions are devised to bring those costs back down. The whole apparatus of property rights, contract law, standards, and certification exists, in North's reading, to make impersonal exchange cheap enough to be worth undertaking.

An open-data policy is an institution in precisely North's sense, and its effect runs through the transaction-cost channel he identifies. The steps a prospective data user must complete correspond structurally to the cost categories he names. Under a restricted-access regime, a researcher who is not part of the mission team must locate the relevant data, establish eligibility to receive them, negotiate or pay for access, accept and comply with license terms, and acquire the tooling to read and interpret the product. Each step is a transaction cost in North's taxonomy: locating and verifying the data is a measurement cost; establishing eligibility and complying with license terms is an enforcement cost. Under a free-and-open regime with persistent identifiers, standard open licensing, and curated products, those costs fall toward the residual cost of downloading a file and learning a documented format. The inference from this correspondence to the policy's effect rests on North's own proposition that lowering the transaction cost of impersonal exchange raises its volume; if the proposition holds for the exchange of goods across a market, it holds for the exchange of data across a research community, because the cost categories are identical in kind. That principle carries weight because of the durability and breadth of North's framework, which has organized a generation of work on the relationship between institutions and economic performance and which rests on the prior Coasean result that, absent transaction costs, the allocation of resources is independent of the assignment of rights, so that it is precisely the transaction costs institutions reduce that determine real outcomes [\[85\]](#ref-85).

One condition on this claim is important and must be protected. The prediction is conditional, not unconditional. It states that lowering access cost raises impersonal use *if access cost was a binding constraint on that use*. If the binding constraint lies elsewhere (in funding for analysis, in the maturity and usability of the data product, or in the sheer size of the latent user community), then lowering access cost may produce little or no rise in downstream use, and the framework predicts a null. This is not a weakness of the framework; it is the framework correctly specifying the condition under which its prediction is testable. The obvious objection is that the apparent rise in use after a policy change could be driven by a confound that moves with the policy (a mission maturing, a community growing, a concurrent funding increase) rather than by the access-cost channel. North does not dispose of that objection at the level of theory; it is resolved at the level of design, in the matched, staggered identification strategy that Section 2.4 motivates and Chapter 5 specifies. Confidence in the claim that open data is a transaction-cost-reducing institution is high, because the correspondence to North's categories is structural and not merely analogical. Confidence that the access-cost channel is the *operative* one in any given mission is moderate at the framework stage and is exactly what the empirical design is built to test.

### 2.1.2 The named mechanism, not a bare correlation

A causal claim earns its standing only when it names a mechanism running from driver to observable effect to operational consequence, never a bare correlation. The mechanism this anchor supplies is the following chain. The driver is the institutional rule change: a mission transitions from restricted or fee-based access to free-and-open release under a standard license with persistent identifiers. The proximate effect is a fall in the transaction cost a prospective non-team user faces, decomposed into the measurement cost of finding and verifying the data and the enforcement cost of obtaining and complying with access terms. The first observable consequence is a rise in the volume of access events, because the users for whom the cost previously exceeded the expected benefit now find the exchange worthwhile; this is observable in distribution and download logs and should appear early, since downloading is the act most immediately responsive to a price change. The second observable consequence, lagged behind the first, is a rise in impersonal downstream use: publications by researchers with no prior mission-team affiliation who obtain the now-cheap data, analyze them, and publish. The third observable consequence, lagged further and emerging only in the later part of the window, is a rise in formal citation to the mission's datasets as first-class scholarly objects, as data-citation norms diffuse [\[27\]](#ref-27), [\[33\]](#ref-33)]. The operational consequence is that the scientific return on the mission's data investment, realized through impersonal reuse, rises. The strategic implication is that NASA and JPL can, in principle, weigh the cost of open-release infrastructure against a measured rather than asserted yield, located in event time and decomposable by sensor class.
This is a mechanism and not a correlation because each link names a specific channel through which the prior link operates and predicts a specific, separately observable signature. The signature is what makes the mechanism falsifiable. If the access-cost channel is real, distribution must move before publications move, because the cost change acts on the download decision before it can act on the publication decision that downloads enable. A publication rise unaccompanied by any distribution rise is therefore not merely unexplained; it is positively evidence *against* the mechanism, because it severs the chain at its first link, and Section 2.2 will show that under the Kuznets discipline such a pattern is the signature of relabeling rather than new use. The temporal ordering of the signatures does real inferential work: it is the within-design check that distinguishes the named mechanism from a spurious co-movement.

### 2.1.3 Path dependence and the gradual-adjustment expectation

North's framework supplies a second prediction beyond the direction of the effect, and it concerns the effect's shape over time. North devotes substantial attention to path dependence: institutions and the organizations that form around them constitute an inherited matrix that constrains the present, so that change is incremental and the response to a new rule is conditioned by the structures the old rule produced. For the present study this implies that the response to open-data release should be gradual and cumulative rather than instantaneous. A research community that grew up under restricted access will have built workflows, intermediary relationships, and expectations adapted to that regime: data-access brokers, institutional subscriptions, established collaborations with the mission team, and a tacit sense among outsiders that the data are hard to get and therefore not worth pursuing. North's path-dependence proposition supplies the logic. Inherited institutional structures persist and condition adjustment, so the full behavioral response to a rule change unfolds over multiple periods as workflows are rebuilt, new entrants discover the now-cheap resource, and the reputation of the data as accessible diffuses through the community. The broad empirical record across institutional economics supports this expectation, finding that responses to rule changes are sluggish and build over time. So does the study's own domain: in the Landsat episode, distribution and publication continued to climb for years after the 2008 policy change rather than jumping once and leveling [\[122\]](#ref-122), [\[132\]](#ref-132)].

The rate of adjustment is itself heterogeneous and unknown at the framework stage. A mission whose latent user community is large, sophisticated, and already primed to use similar data (optical imagery being the canonical case) may adjust quickly; a mission serving a small or specialized community may adjust slowly or barely at all. The objection the framework must pre-empt is that a gradual post-policy rise could equally be produced by a slow-moving confound such as mission maturation, which also builds over time. This is the most dangerous rival for the gradual-adjustment prediction precisely because the two predictions have a similar shape. The framework cannot dispose of it; the design must, by treating mission age as both a matching covariate and a control and by requiring that the pre-policy trend be flat before any post-policy rise is interpreted. The methodological consequence of the gradual-adjustment prediction settles the choice of estimand. Because the framework predicts a dynamic path rather than a one-time jump, the empirical object must be a sequence of event-time coefficients capable of representing a build-up, not a single difference that would average the build-up away. Section 2.4 develops this consequence in full. Confidence in the gradual-adjustment prediction is moderate: it is well-motivated by theory and consistent with the Landsat record, but the alternative maturation explanation has a similar signature and can be separated only by design, not by theory.

### 2.1.4 Nominal versus functional openness: the FAIR construct-validity discipline

North's framework also imposes a discipline on how the treatment itself is defined, and this discipline protects the study against mislabeling its own independent variable. North insists that an institution is justified by the transaction cost it actually lowers, not by its label. A rule that is nominally open but functionally encumbered (open in license but practically inaccessible because the data lack persistent identifiers, machine-readable metadata, documented formats, or the tooling needed to use them) has not lowered the relevant cost and should not be coded as treated. The treatment variable must therefore be operationalized in terms of functional rather than nominal openness. The transaction cost North's mechanism acts upon is the *total* cost of finding, verifying, obtaining, and reusing the data, and a policy that removes the licensing barrier while leaving the findability and usability barriers in place has removed only one component of that cost. The FAIR Guiding Principles of Wilkinson and colleagues [\[120\]](#ref-120) give this distinction operational content, decomposing data accessibility into Findability, Accessibility, Interoperability, and Reusability and thereby separating a dataset that is merely licensed-open from one that is genuinely cheap to reuse. Subsequent development of the FAIR principles reinforces the point: Mons and colleagues clarify that FAIRness is a property of the data and its surrounding infrastructure rather than a binary open-or-closed switch, and emphasize that "increasingly FAIR" is the realistic target, so that openness is a gradient and not a dichotomy [\[9\]](#ref-9); Barker and colleagues extend the principles to research software, showing that reusability depends on the tooling around the data and not only on the data themselves [\[80\]](#ref-80).

The transfer to the present design is direct and consequential. Coding a mission as "treated" on the date its license changed, while ignoring whether persistent identifiers, documented products, and access tooling were in place, would introduce a treatment that is nominal rather than functional and would attenuate or distort the estimated effect by mixing genuine cost reductions with cosmetic ones. The design therefore records, in the hand-coded adoption register, not only the license-change date but the findability, interoperability, and reusability status before and after, and a robustness specification reclassifies missions coded as open but functionally encumbered. Functional openness is a matter of degree and its coding involves judgment, which is why the register is double-entered and adjudicated and why the encumbered-reclassification is a robustness check rather than the primary specification. This operationalization answers the construct-validity objection that the study measures a label rather than a treatment, since the FAIR decomposition ties the treatment to the cost it actually lowers. A complementary line of evidence holds that functional accessibility, not nominal openness, is what drives use: Demetres and colleagues, reviewing the impact of institutional repositories, find that the realized benefit of openness depends on the infrastructure that makes deposited material findable and usable rather than on the bare fact of deposit [\[79\]](#ref-79). Confidence in the claim that the treatment must be functional rather than nominal is high; confidence that any particular mission's functional-openness coding is correct is moderate and is protected by the double-entry, adjudication, and robustness machinery.

## 2.2 Kuznets and the measurement lens: the outcome as a constructed proxy

### 2.2.1 The framework and its lineage

The second anchor is the measurement discipline of the national-accounts tradition that Simon Kuznets founded. Kuznets built the architecture of national income accounting in the 1930s and 1940s and insisted, against the temptation to treat the aggregate as the thing itself, that a national income figure is a construction: a deliberate choice about what to count, how to value it, and where to draw the production boundary, and therefore a proxy for an underlying welfare or output concept rather than a direct reading of it. The Kuznets lineage matters here because the study's outcome variables (publication counts and dataset-citation counts) are exactly this kind of construction: deliberate aggregations that stand in for the latent quantity of scientific productivity but are not identical to it. The bibliometric outcomes must therefore be treated as constructed proxies with a stated, biased error structure, and a movement in the proxy is not evidence of a movement in scientific productivity until the proxy's known biases have been accounted for.

The basis for this position is the structural parallel between a national income aggregate and a citation count. Landefeld, Seskin, and Fraumeni, writing in the Kuznets tradition about how gross domestic product is measured, make the general point explicit: an aggregate such as GDP is an indicator assembled from many imperfect source data under a set of conventions, and the conventions shape what the indicator can and cannot show, so that the figure is a measured construct whose construction must be understood before it is interpreted [\[62\]](#ref-62). A citation count is assembled in exactly the analogous way: it is a count of a particular kind of recorded event (a formal reference), captured by a particular indexing infrastructure (a bibliographic database with its own coverage rules), under a particular set of attribution conventions, and it therefore inherits the same status as a constructed indicator rather than a direct measurement of intellectual influence or scientific use. Two records reinforce the parallel: the national-accounts tradition has long treated its own aggregates as provisional and convention-laden, and scientometrics has established that citation counts are right-skewed, accumulate with a lag, depend on field size and citation norms, and are sensitive to the coverage of the source database. None of this makes the proxy useless; a proxy can still be informative despite its biases, provided the biases are stated and, where possible, differenced out, so the Kuznets stance is not nihilism about measurement but discipline about it. What it forbids is the naive reading in which "more citations" is simply equated with "more science," at least until the proxy's error structure has been addressed.

### 2.2.2 The satellite-proxy analogue as proxy discipline

The Kuznets measurement stance has a direct and unusually apt analogue in the satellite-remote-sensing literature, fitting for a dissertation about Earth-observation missions. Henderson, Storeygard, and Weil use night-time lights observed from satellites as a proxy for economic activity, and their methodological contribution is not the proxy itself but the disciplined way they treat it [\[41\]](#ref-41). The night-lights study is the model for how this dissertation should handle its own proxies. The Henderson, Storeygard, and Weil approach does not assert that night-lights *are* economic output; it treats night-lights as a noisy measurable indicator, recognizes that the conventional income measure it wishes to improve is *also* noisy, and develops a framework that optimally combines the two imperfect measures rather than privileging either as truth. This is the correct general posture toward any proxy: name the error structure, refuse to treat the indicator as the latent quantity, and triangulate across imperfect measures rather than trusting one. The influence and durability of the night-lights framework as a template for proxy-based inference in economics and Earth science lends the posture its standing.

The transfer to the present design is concrete and shapes the data architecture of Chapter 4. Just as Henderson, Storeygard, and Weil combine two imperfect measures, this study refuses to rest its outcome on a single bibliographic database; it draws publication and citation counts from both the NASA Astrophysics Data System [\[60\]](#ref-60) and Web of Science and cross-checks them, on the explicit reasoning that a result appearing in one source but not the other is more likely an indexing artifact than a real change in output. The dual-source design is the bibliometric analogue of triangulating across noisy proxies. The study also treats distribution-log volume as a third, independent proxy that is upstream of publication and arises from a different recording infrastructure entirely, so that agreement among distribution, publication, and citation movements is the kind of cross-proxy corroboration the night-lights framework recommends, and disagreement among them is the kind of warning the framework is designed to surface. One caveat is that triangulation reduces but does not eliminate proxy error; correlated biases across sources (for example, a field-wide change in citation norms that affects both ADS and Web of Science) survive triangulation and must be addressed by other means, principally the frozen counting rule discussed below. Confidence in the value of the multi-proxy posture is high; it is a direct application of an established and influential template.

### 2.2.3 Real output versus relabeling: the within-versus-reallocation distinction

The most consequential discipline the Kuznets lineage imposes is the requirement to distinguish a real increase in output from a mere relabeling of existing output. An apparent rise in mission-linked publications after open release could reflect either genuinely new research that would not have occurred under restricted access, or a change in how pre-existing research is attributed and counted, and the two must be separated before the rise can be read as a productivity gain. The reason to take the relabeling possibility seriously comes from McMillan and Rodrik, who decompose aggregate productivity growth into a within-sector component (genuine productivity improvement inside sectors) and a structural-change or reallocation component (movement of resources between sectors), and show that what looks like aggregate transformation can be reallocation that does not, by itself, represent new productive capacity [\[76\]](#ref-76). The same decomposition logic applies to a citation count: the post-policy total can rise because new work is being done (the analogue of within-sector improvement) or because existing work is being re-attributed to the mission as data-citation norms make naming the dataset easier and more expected (the analogue of reallocation or relabeling). The within-versus-between distinction is central across the productivity-measurement literature, and McMillan and Rodrik show specifically that conflating the two yields a misleading picture of growth.

The relabeling mechanism in this setting is specific and plausible, which is why it must be designed against rather than waved away. As formal data-citation norms diffuse [\[27\]](#ref-27), [\[33\]](#ref-33)], authors who would previously have used a mission's data with only an informal acknowledgment, or with no machine-detectable trace at all, increasingly name the dataset explicitly and cite it as a first-class object. A bibliometric pipeline that detects mission linkage partly through dataset-identifier matching will therefore count *more* mission-linked publications over time even if the underlying volume of research using the data is constant, simply because the same research is now more detectable. This is the relabeling channel, and it is confounded with the treatment because both the policy change and the rise of data-citation norms are concentrated in the later part of the window. The design's primary defense, derived directly from this Kuznets discipline, is to hold the bibliographic matching rule *fixed* across the pre- and post-adoption periods, so that a change in detection practice cannot masquerade as a change in output; a supplementary defense restricts the outcome to publications by authors with no prior mission-team affiliation, isolating impersonal use in North's sense and removing the part of the count most exposed to attribution drift. The decisive design check, however, is the cross-proxy one already introduced: because real new use must pass through the distribution channel (a new user must obtain the data before publishing with them), a publication rise that is genuine should be preceded by a distribution rise, whereas a publication rise that is pure relabeling need not be, because relabeling re-attributes work whose data were already obtained. A publication rise with no accompanying distribution rise is therefore, under the joined North-Kuznets logic, the signature of relabeling and falsifies the productivity interpretation. This check is necessary but not sufficient; distribution logs have their own coverage gaps and a weak distribution signal may reflect log incompleteness rather than relabeling, which is why the distribution arm is treated as a mechanism check and an early-response descriptor rather than as a primary outcome. Confidence in the importance of the relabeling threat is high; confidence that the design fully neutralizes it is moderate, bounded by the quality of the distribution logs and the linkage rule.

### 2.2.4 The fragile-aggregate caution

The Kuznets lineage carries a final, sobering discipline: aggregate empirical relationships that appear robust can prove fragile once subjected to scrutiny over specification, comparison group, and the definition of the variables. The standing example within this lineage is the environmental Kuznets curve, an inverted-U relationship between income and pollution that looked robust in early cross-sections and then proved sensitive to omitted variables, functional form, and heterogeneity once reexamined. This dissertation's headline estimate, whatever its sign, must be held to the same scrutiny and reported as provisional until it survives. The historical record within the Kuznets tradition is full of aggregate relationships that did not survive reexamination, of which the environmental Kuznets curve is the most cited instance. An aggregate causal estimate is only as credible as its robustness to the choices that produced it, so a single point estimate, however precise, is not yet a finding. The broad methodological consensus that robustness reporting is a precondition for credible aggregate inference is one this study honors by specifying its robustness battery in advance rather than after seeing the primary result.

The transfer to the design is the commitment to report the effect as a robustness region rather than a single number. The Rambachan and Roth sensitivity analysis [\[97\]](#ref-97), discussed in Section 2.4 and specified in Chapter 5, reports how large a violation of the identifying assumption would be required to overturn the estimate, converting the headline into a region of values consistent with the data under stated assumptions. The pre-specified family of heterogeneity-robust estimators [\[14\]](#ref-14), [\[30\]](#ref-30), [\[62\]](#ref-62), [\[113\]](#ref-113)] provides a second layer of scrutiny: agreement across estimators chosen in advance is informative, whereas agreement engineered after the fact is not. No amount of robustness reporting can rescue an estimate from a fundamental identification failure (a violated parallel-trends assumption voids the causal reading regardless of how the robustness region looks), which is why the leads test in Section 2.4 is logically prior to the sensitivity analysis. This discipline pre-empts the specification-search critique: that an analyst who tries enough specifications will find a significant effect. The defense is pre-registration of the outcome definitions, the matching procedure, the estimator set, the event-time window, and the decision rule before estimation, so that the robustness checks are confirmatory rather than exploratory. Confidence in the fragile-aggregate caution is high; it is a hard-won lesson of the measurement tradition and is precisely why the study's deliverable is a pre-registered design rather than a result.

## 2.3 The integrated conceptual model the empirical work tests

### 2.3.1 Fusing the mechanism and the measurement stance

The two anchors are not parallel ornaments; they interlock to produce a single conceptual model, and the interlock is the chapter's central theoretical contribution. North supplies the causal chain and its predicted shape; Kuznets supplies the instrumentation of that chain through proxies whose error structure is named, and the test that distinguishes a real movement along the chain from an artifact of measurement. The object the empirical chapters test is the conjunction: a North causal chain observed through Kuznets proxies, in which the temporal ordering predicted by the mechanism doubles as the check that the measurement requires. The two frameworks share the same observable surface (the rise or non-rise of bibliometric and distribution indicators) and impose complementary, non-redundant requirements on how that surface is read. A model that specifies both the mechanism and the proxy error structure can convert a pattern of co-movements into evidence about a latent causal quantity, whereas either framework alone cannot: North without Kuznets would credulously read any post-policy rise as a productivity gain, and Kuznets without North would correctly distrust the proxies but would lack the mechanism that tells the analyst what temporal signature a real effect must have.

The integrated chain, stated as the conceptual model, runs as follows. A mission adopts free-and-open, functionally FAIR release (the North rule change, coded for functional rather than nominal openness). The transaction cost of obtaining and reusing the data falls (the North proximate effect, unobserved directly but inferred). Distribution and download volume rises first (the first observable, a Kuznets proxy drawn from Earthdata and DAAC logs, whose biases are log-coverage gaps and double-counting of automated retrievals). Impersonal publication by non-team authors rises next, after the lag required for obtained data to become analyzed and published (the second observable, a Kuznets proxy drawn from ADS and Web of Science under a frozen matching rule, whose biases are right-skew, citation and publication lag, field-size dependence, and indexing coverage). Formal dataset citation rises last and only in the later window (the third observable, a Kuznets proxy whose additional bias is the sparsity and recency of data-citation practice). At each node the proxy's error structure is stated in advance, and the predicted temporal ordering (distribution before publication before dataset citation) is the within-model check that a real movement along the North chain, rather than a relabeling or an indexing artifact, has occurred. The model is a set of conditional predictions, not a guarantee; each link holds only if access cost was the binding constraint and if the proxy biases behave as stated. The objection it must answer (that the whole pattern is produced by a confound moving with the policy) belongs to the identification strategy, not the conceptual model, and Section 2.4 hands the problem to it. Confidence in the integrated model as a *framework* is high; confidence in any *instantiation* of it for a given mission is conditional and moderate, exactly as the design-stage evidence grade requires.

### 2.3.2 The proxy error structure, made explicit node by node
The Kuznets discipline forbids leaving the proxy error structure implicit, so the conceptual model states it at each node. For the distribution proxy, the error structure is this: download logs over-count automated and machine-to-machine retrievals relative to substantive human use, under-count use mediated through cloud-hosted analysis that never triggers a download event, and have coverage that changes as data systems migrate. For inference this means distribution volume is a usable early-response and ordering signal but a poor absolute measure, which is why it serves as a mechanism check rather than a primary outcome. For the publication proxy, the error structure is fourfold: counts are right-skewed because a few datasets attract most use; they accumulate with a lag of years between data access and publication; they depend on the size and citation norms of the field, so that an identical scientific contribution generates more recorded publications in a large, fast-citing field than in a small, slow-citing one; and they are sensitive to the coverage of the indexing database, which changes over time and differs between ADS and Web of Science. Four consequences follow for inference. The count model must accommodate skew and structural zeros. The lag must be represented in the event-time window rather than expected at event time zero. Field heterogeneity must be addressed by within-mission and within-stratum comparison rather than cross-field pooling. And the dual-source cross-check is required to separate indexing artifacts from real change. For the dataset-citation proxy, the error structure adds that formal data citation is sparse and recent, so the proxy carries low statistical power early in the window and is analyzed separately, with explicit power caveats, rather than pooled with publication counts.

Stating the error structure in advance is a design input rather than a disclaimer: each named bias maps to a specific design feature that addresses it. The correspondence is the one just enumerated, one to one: skew to count model, lag to event-time window, field dependence to within-stratum comparison, indexing sensitivity to dual sources, data-citation sparsity to separate analysis with power caveats. This follows the Kuznets principle that a proxy's construction shapes inference, so the construction must be made explicit and its implications carried into the design [\[62\]](#ref-62), and the applied demonstration in the night-lights framework bears it out: naming a proxy's noise and designing around it yields credible inference where treating the proxy as truth would not [\[41\]](#ref-41). Some biases correlate with the treatment timing (the rise of data-citation norms is the leading example) and cannot be differenced out by the within-stratum comparison alone; these require the frozen counting rule and the no-prior-affiliation specification. Confidence in the completeness of the stated error structure is moderate. The listed biases are the principal known ones, but the Kuznets posture itself counsels that unstated biases may remain, which is why robustness and sensitivity reporting belong to the model rather than being added afterward.

### 2.3.3 How the conceptual model carries the larger argument

The conceptual model is where the dissertation's central argument comes into focus, and stating it here keeps the later chapters honest. Several commitments run through the model, each of which it either establishes or hands forward. The question is a live one: data-access policy sits on the causal path between a mission and its scientific return, and openness is repeatedly associated with more downstream use [\[19\]](#ref-19), [\[75\]](#ref-75), [\[96\]](#ref-96), [\[122\]](#ref-122), [\[132\]](#ref-132)], a path the conceptual model establishes theoretically through the North chain. It is also consequential in magnitude: the Landsat free-and-open switch was followed by an order-of-magnitude rise in distribution and a sharp expansion in publications and operational products [\[77\]](#ref-77), [\[122\]](#ref-122), [\[132\]](#ref-132)], and free-and-open satellite data carry first-order, measurable value for downstream science and application, as documented for biodiversity conservation by Turner and colleagues [\[121\]](#ref-121); the conceptual model locates that consequence in the size of the transaction cost being removed. The model then specifies the access-cost channel and its temporal signature, handing the isolation of that channel from confounds to the identification strategy, and it shows why an article-level association cannot remove author self-selection and why a single-mission before-and-after cannot separate the policy from secular trends, which is what motivates the matched, staggered, multi-mission design that Section 2.4 introduces. It states the proxy biases (Kuznets), names the relabeling threat and the design features that address it, and commits to reporting the effect as a robustness region rather than a point. Each of these commitments is either argued in this chapter or explicitly forwarded to a named later chapter, so that the argument remains continuous from framework to conclusion. The last of them, the acceptability of what cannot be ruled out, is a design-stage judgment rather than a post-estimation finding, and is calibrated accordingly.

## 2.4 From framework to estimand: why the mechanism implies a dynamic event-study path within matched strata

### 2.4.1 The framework dictates the shape of the empirical object

The final task of this chapter is to bridge from the conceptual model to the empirical object the later chapters estimate, and the bridge carries weight: the choice of estimand is not a methodological preference imposed from outside but a direct consequence of the framework built above. The North-Kuznets conceptual model implies a dynamic event-study path of treatment effects within matched strata, and forbids both a single pooled before-and-after difference and a naive two-way fixed-effects regression. Three features of the conceptual model establish this. First, North's path-dependence prediction is that the response builds over multiple post-policy periods rather than appearing as a one-time jump, so the empirical object must be able to represent a build-up, which a sequence of event-time coefficients can and a single difference cannot. Second, the Kuznets relabeling and confound concerns require a check on whether the outcome was already trending up before the policy, which only the pre-policy leads of an event study can provide; a single before-and-after difference has no leads and cannot perform the check. Third, the heterogeneity built into the model (the effect is expected to differ by sensor class and to grow at different rates across missions) means the estimand must accommodate heterogeneous, dynamic effects rather than impose a single common effect.

What connects these features to the choice of estimand is supplied by the modern difference-in-differences literature. Callaway and Sant'Anna define the group-time average treatment effect on the treated, \(\operatorname{ATT}(g,t)\), for adoption cohort \(g\) and period \(t\), and aggregate it into a dynamic event-study path indexed by event time and into an overall summary, by construction robust to treatment-effect heterogeneity across cohorts and over event time [\[14\]](#ref-14). This is the object the conceptual model demands: it represents the build-up (the event-time path), supplies the pre-policy leads (the pre-trend check), and tolerates heterogeneity (cohort-specific effects). The choice is grounded in Goodman-Bacon's demonstration that the naive two-way fixed-effects estimator, which the conceptual model's heterogeneity would otherwise invite, is unreliable under staggered timing because it implicitly uses already-treated units as controls and can place perverse, even negative, weights on individual comparisons [\[35\]](#ref-35). Sun and Abraham show the same pathology for event-study coefficients estimated by the conventional regression and propose an interaction-weighted alternative [\[113\]](#ref-113), and de Chaisemartin and D'Haultfoeuille establish the general result that two-way fixed-effects estimators are weighted sums of treatment effects with weights that can be negative [\[30\]](#ref-30). The Callaway-Sant'Anna estimand identifies the causal effect only under its own assumptions (conditional parallel trends and no anticipation), which the design must defend rather than assume. These results answer the natural objection that one could simply run a standard fixed-effects regression on the panel; the econometric literature shows why that would be biased under exactly the conditions the conceptual model predicts. Confidence that the framework dictates a dynamic, heterogeneity-robust event-study path is high, because the implication is logical given the framework and is corroborated by an established econometric literature.

### 2.4.2 Why matched strata, and the identifying assumption stated honestly

The conceptual model implies not only a dynamic estimand but a matched one, and the reason is the confound the model itself names. The event-study path must be estimated within strata matched on sensor class and mission age, and the identifying assumption is conditional parallel trends within those strata. The model's principal rival explanation is maturation (output rises because missions mature, not because they go open) and selection on trends (missions go open precisely when their output is already rising), both of which produce a post-policy rise that mimics the treatment effect. Matching addresses these by comparing an open optical imager with restricted optical imagers of similar age, rather than with the full and heterogeneous pool of all missions, so that the comparison holds fixed the sensor class and maturation stage that drive the confound. The propensity-score framework of Rosenbaum and Rubin establishes that conditioning on a balancing score renders treatment assignment ignorable under stated assumptions [\[99\]](#ref-99), and Stuart's matching guidance on constructing credible comparison groups [\[111\]](#ref-111) and the covariate-balancing extension of Imai and Ratkovic that estimates the propensity score so as to optimize covariate balance directly [\[59\]](#ref-59) make the procedure operational. The balance-diagnostic machinery of Austin then quantifies, through standardized differences, whether the matched comparison group is in fact comparable on the observed covariates [\[8\]](#ref-8), so that the plausibility of the identifying assumption can be reported rather than merely asserted.

The identifying assumption must be stated honestly, because its honesty is the difference between an identified estimate and a dressed-up correlation. The assumption is that, conditional on the matching covariates, the publication and citation trajectories of treated missions would have evolved in parallel to those of their matched comparison missions in the absence of the policy. This is an assumption about a counterfactual that is never observed and therefore cannot be proven; it can only be made plausible and probed. The conceptual model probes it in two ways. The pre-policy leads of the event study test directly for differential pre-trends: under valid identification, the leads should be flat, and positive trending leads are a specific falsifier that voids the causal interpretation regardless of the sign of the post-policy lags. Roth shows that the power of this pre-trend test is itself limited and that conditioning on having passed it can distort the estimates, so the test must be read with the power diagnostics he supplies rather than as a clean pass-fail [\[100\]](#ref-100). Rambachan and Roth then convert the residual uncertainty into a reported quantity: rather than assuming exact parallel trends, they ask how large a violation of parallel trends would have to be, relative to the observed pre-trends, to overturn the estimated effect, and report the answer as a breakdown threshold and a robustness region [\[97\]](#ref-97). The limitation carried throughout is that identification rests on an untestable assumption made plausible by matching and probed by the leads and the sensitivity analysis, not proven; the causal claim is therefore conditional, and its confidence is calibrated to the strength of that conditioning. Confidence in the appropriateness of the matched, conditional-parallel-trends design is high; confidence in the causal interpretation of any particular estimate it would produce is, by construction, conditional and is reported as a region under sensitivity analysis rather than as a certainty.

### 2.4.3 The estimand stated in the study's fixed notation

To close the bridge and ensure consistency with the chapters that follow, the estimand is stated in the notation fixed for the whole dissertation. For adoption cohort g (the set of missions adopting free-and-open release in period g) and period t, the primary estimand is the Callaway and Sant'Anna group-time average treatment effect on the treated,

\[
\operatorname{ATT}(g,\,t) = \mathbb{E}\!\left[\, Y_t(g) - Y_t(0) \mid G = g \,\right] \qquad\qquad (1)
\]

where \(Y_t(g)\) is the potential outcome under adoption in period \(g\), \(Y_t(0)\) is the never-treated potential outcome, and \(G\) is the adoption cohort. \(\operatorname{ATT}(g,t)\) is identified by comparing the change in outcome for cohort \(g\) from period \(g-1\) to \(t\) against the same-calendar change for a comparison group of not-yet-treated and never-treated missions, within matched sensor-class-by-age strata. The \(\operatorname{ATT}(g,t)\) are aggregated into a dynamic event-study path indexed by event time \(e = t - g\),

\[
\theta(e) = \sum_{g} w_{g} \cdot \operatorname{ATT}(g,\, g+e) \qquad\qquad (2)
\]

with cohort weights \(w_g\) proportional to cohort size, and into an overall summary effect. The last pre-adoption period (\(e = -1\)) is normalized to zero. Leads (\(e < 0\)) test pre-trends; lags (\(e \geq 0\)) trace the dynamic effect. Outcomes are modeled in a count-appropriate form (Poisson or log-link, with attention to the structural zeros common for small or young missions), and standard errors are clustered at the mission level with a wild-cluster bootstrap given the modest number of cohorts.

The conceptual model maps onto this notation cleanly, which is the point of building it. The North path-dependence prediction is the prediction that the lags \(\theta(e \geq 0)\) rise over event time rather than jumping and leveling. The pre-trend and selection-on-trends concerns are the requirement that the leads \(\theta(e < 0)\) be flat. The heterogeneity built into the model is the cohort-and-event-time structure of \(\operatorname{ATT}(g,t)\) that the Callaway-Sant'Anna estimand preserves rather than averages away. The Kuznets relabeling check is external to this notation and lives in the cross-proxy comparison: a publication \(\theta(e)\) path that rises without a corresponding distribution \(\theta(e)\) path rising earlier is read as relabeling and falsifies the productivity interpretation. The falsification rule the whole dissertation is built around follows directly: support for H1 requires flat leads, positive lags with a positive and significant overall effect, and survival of the Rambachan-Roth sensitivity analysis at the stated breakdown threshold; failure of any one falsifies the contribution, and positive trending leads void identification before the lags are even examined. The qualifier, stated once more because the design stage requires it, is that every \(\theta(e)\) and every \(\operatorname{ATT}(g,t)\) referred to in this chapter is a population estimand whose sample analogue has not been computed; no coefficient is reported, and the path's illustrative shape (flat leads, rising lags, larger for optical imagers) is a prediction of the framework, explicitly labeled as such and not an estimate.

### 2.4.4 A note on scope

One framing decision must be recorded to keep the chapter disciplined. This is an econometric policy-evaluation dissertation, and it does not produce a systems or capability architecture; there is no capability, system function, or data-service exchange being designed here. What matters, stated plainly, is the link between the study's objective and the decision it informs: the objective is to maximize the scientific return on NASA's and JPL's investment in Earth-observation missions, and the decision the evidence is meant to inform is whether and when to fund free-and-open data release and the supporting data-system infrastructure at mission formulation. The chapter offers an argument about a mechanism and its measurement, not a system design, and this scope is recorded here so that no later chapter reintroduces system-design vocabulary by default.

## 2.5 Summary of the framework and its forward commitments

The chapter has built the conceptual apparatus the empirical work will test, and it closes by stating what that apparatus commits the later chapters to. From North, the study takes the mechanism: free-and-open, functionally FAIR data release is an institutional rule change that lowers the transaction cost of impersonal exchange and should, if access cost was the binding constraint, raise impersonal downstream use through a path-dependent, gradual response whose first signature is a rise in distribution. From Kuznets, the study takes the measurement discipline: the bibliometric outcomes are constructed proxies with a stated, biased error structure, a rise in the proxy must be shown to be real new use rather than relabeling before it is read as productivity, and the headline effect must be reported as a robustness region rather than a point. The integrated conceptual model fuses the two into a single chain (rule change to falling access cost to rising distribution to rising impersonal publication to rising dataset citation), instruments each node with a named proxy, and uses the mechanism's predicted temporal ordering as the measurement check the proxies require. The bridge to the estimand then follows by necessity rather than choice: the path-dependence prediction, the pre-trend check, and the built-in heterogeneity together dictate a dynamic, heterogeneity-robust event-study path within matched strata, formalized as the Callaway-Sant'Anna group-time ATT, defended by matching and conditional parallel trends, and probed by the leads and the Rambachan-Roth sensitivity analysis.

The forward commitments are explicit. Chapter 3 will situate this framework in the empirical literature on the open-access and open-data citation advantage, showing how the article-level evidence motivates the mechanism while its self-selection vulnerability motivates the move to the mission level. Chapter 4 will operationalize each proxy node of the conceptual model, naming the sources, the coverage, and the biases, and will build the measurement table the Kuznets discipline demands. Chapter 5 will specify the estimator, the matching, the identification assumptions, and the threats-to-validity defenses that this chapter has motivated. Chapter 6 will state the pre-registered analysis plan and the falsification rule in full, with result tables specified but, by design, unpopulated. The confidence the framework supports is stated plainly and is carried forward unchanged: the design supports, at best, a conditional and moderate-confidence causal reading, raised by flat leads and a surviving sensitivity region and an accompanying distribution rise, and lowered by trending leads, a fragile sensitivity region, or a publication rise without a distribution rise. The framework is complete; no result has been computed; the contribution is the design and its falsification conditions, exactly as the study set out to deliver.


# Chapter 3: Literature Review
## 3.0 Overview: what the literature establishes and where it falls short

The literature converges on a single proposition that this dissertation can both lean on and improve: openness is repeatedly associated with greater downstream use of scholarly outputs, but the evidence that establishes the association is almost entirely measured at the wrong unit and almost entirely unable to rule out the explanation that would make it spurious. The proposition is stated at the outset so the review that follows can be read against it. The open-access and open-data literatures establish a replicated, economically meaningful base rate: articles and datasets that are open accrue more citations and more reuse than those that are not. The systematic-review literature establishes, with equal force, that this base rate is contaminated by author self-selection, field heterogeneity, funding, and topic, so that the magnitude is contested and the causal reading remains unproven at the level where it has been measured. The mission-level remote-sensing literature establishes that a single program-level policy switch, Landsat in 2008, was followed by an order-of-magnitude change in distribution and a structural change in the publication record. This demonstrates that the mechanism operates at the level of a data producer and not only at the level of an individual author choice. What no body of work in the corpus does is combine the two: treat the mission as the unit of analysis, treat the mission's transition to free-and-open release as a policy event rather than an author decision, and apply a heterogeneity-robust, matched, staggered difference-in-differences design that can separate the policy effect from secular trends and from the maturation of the mission itself. That combination is the gap, and the propositions that follow from it are the bridge from this chapter to the design in Chapters 5 and 6.

The problem this chapter addresses comes into focus along the same line as the rest of the dissertation. What the field knows is a large, internally consistent article-level and dataset-level literature on the open-access citation advantage and the open-data citation advantage, paired with a smaller, less consistent literature on data-citation practice and a handful of program-level remote-sensing case descriptions. What it lacks is a literature that supports an identified, mission-level estimate of the scientific yield of open release, located in event time and decomposed by sensor class, against which the cost of open-release infrastructure can be weighed. No study in the assembled corpus treats the mission as the treated unit under a policy-event design; the closest precedents are descriptive single-program narratives without a contemporaneous control. As long as that absence persists, NASA, the Jet Propulsion Laboratory, and the Science Mission Directorate continue to credit or discredit free-and-open data policy on anecdote and on episodes, and the binding constraint on a mission's scientific yield, whether access cost, analysis funding, product maturity, or community size, is never separated. This chapter reads the literature to that end: not to celebrate the open-access advantage but to locate where its evidentiary foundation is strong, where it is weak, and what design those strengths and weaknesses jointly imply.

The chapter is organized thematically rather than chronologically. Section 3.1 reviews the open-access citation advantage proper, the core finding and its systematic-review counterweight, and isolates the self-selection threat that dominates every subsequent section. Section 3.2 turns to the open-data and dataset-reuse citation advantage and to the data-citation-practice literature that governs whether a dataset-level outcome can even be measured. Section 3.3 reviews the evidence on field, funding, and topic heterogeneity, which converts a single headline number into a distribution of effects. Section 3.4 examines policy- and mandate-level evidence, where openness is imposed rather than chosen, because that is the design feature that begins to break the self-selection problem and is therefore the closest article-level analogue to the mission-level treatment this dissertation studies. Section 3.5 reviews the mission-level remote-sensing episodes, Landsat and Copernicus uptake, as program-level natural experiments. Section 3.6 synthesizes the two gaps and states the propositions that follow. Throughout, causal claims are tied to a named mechanism rather than left to rest on correlation, and the confidence attached to each is calibrated to the design-stage evidence grade. This is a design-stage document: no result is executed, and the literature is interpreted to specify a design, not to report findings.

## 3.1 The open-access citation advantage: the core finding, the counterweight, and the self-selection threat

### 3.1.1 The core finding

The foundational claim of the open-access literature is simple and has been replicated across two decades, many fields, and several bibliographic databases: articles that are freely available are cited more than articles that are not. Eysenbach [\[32\]](#ref-32) gave the early, influential statement of the claim by comparing open-access and non-open-access articles within the same journal, *Proceedings of the National Academy of Sciences*, and reporting a substantial citation differential in favor of open access in the first months and years after publication. The within-journal design was a deliberate methodological advance because it held the journal, and therefore much of the prestige and selection that operate at the journal level, constant; the comparison was between articles in the same outlet that differed in access status. Eysenbach's finding set the agenda: a citation advantage exists, it is large in the early window, and it must be explained.

The claim has been confirmed repeatedly in narrow, single-venue or single-discipline samples. Lifang and colleagues [\[66\]](#ref-66), analyzing 12,354 original research articles in 93 Oxford Open journals published in 2009, reported an open-access citation advantage of roughly 139 percent over non-open articles, while also finding that the advantage varied sharply by discipline and was negative for humanities journals. Xianwen and colleagues [\[123\]](#ref-123), studying 1,761 *Nature Communications* articles published in 2012 and 2013, confirmed the citation advantage and extended it to article downloads and social-media attention, and observed that open-access articles sustained steady downloads over a long period rather than only in an early burst. Jincong and colleagues [\[48\]](#ref-48), examining the *European Urology* family of journals for articles published in 2021 with a binary logistic regression on Web of Science data, again recovered a positive association between open access and citation. Sahin and colleagues [\[148\]](#ref-148), analyzing 4,691 articles in the *Journal of Craniofacial Surgery* from 2019 to 2023, found that the small open-access fraction, about seven percent of articles, was cited statistically significantly more than the toll-access remainder. These studies differ in field, sample size, and database, and they converge on the same sign.

This convergence supports a careful reading. An open-access citation advantage exists as a measured association, attested by the repeated, same-direction findings across Eysenbach's within-journal *PNAS* comparison [\[32\]](#ref-32), the Oxford Open corpus [\[66\]](#ref-66), the *Nature Communications* corpus [\[123\]](#ref-123), the urology family [\[48\]](#ref-48), and the craniofacial surgery corpus [\[148\]](#ref-148). An association replicated across independent samples, databases, and fields is unlikely to be an artifact of any single sample, and the replication holds even under designs that control the journal, which removes a large class of confounders. One distinction is essential and must be protected: this is a measured association, not a causal effect, and the magnitude is highly variable, from negative in humanities to triple digits in some open journals. The objection, developed in the next subsection, is that the entire pattern is consistent with a non-causal explanation in which better articles are both more likely to be made open and more likely to be cited. Confidence in the existence of the association is high; confidence in any causal reading at the article level is low, and the design implication is that a credible causal estimate must come from a setting where openness is not an article-level author choice.

### 3.1.2 The systematic-review counterweight

The literature contains its own correction. The most authoritative counterweight is the systematic review by Langham-Putrow, Bakker, and Riegelman [\[63\]](#ref-63), which screened a large body of open-access-citation-advantage studies and concluded that, while a majority of studies report an advantage, the result is far from settled: studies that more carefully control for confounders tend to find smaller or null effects, the magnitude is highly field-dependent, and selection bias is pervasive and rarely fully removed. The method of this review, a structured, protocol-driven synthesis rather than a single new bibliometric comparison, is what gives it standing; it aggregates the evidence base rather than adding one more contestable data point to it. Its limitation is the limitation of all systematic reviews: it inherits the heterogeneity and the methodological weaknesses of the studies it includes, and it cannot manufacture identification that the primary studies lack. Its relation to the gap is direct. It tells this dissertation that the article-level evidence base, taken as a whole, cannot support a causal claim, and that the binding obstacle is selection.

Earlier reviews reached compatible conclusions. Davis and Walters [\[94\]](#ref-94), in a critical review of free-access research, reported clear evidence that free access increases downloads but found the citation evidence equivocal, and explicitly raised the possibility that large measured citation advantages are artifacts of failing to control adequately for confounders. Colby Lewis [\[20\]](#ref-20) updated the Davis and Walters review for literature published after 2011 and reached a similarly cautious verdict, while also noting the library-economics stakes of the question. Wagner [\[2\]](#ref-2) and Swan [\[6\]](#ref-6) compiled annotated bibliographies of the early studies and documented both the breadth of the literature and the inconsistency of its methods and conclusions. Andrew Plume [\[7\]](#ref-7), writing in *Nature*, summarized the state of play with the flat statement that the open-access citation advantage is unproven, a one-line distillation of two decades of contested measurement. The synthesis these reviews jointly produce is that the existence of an association is well attested and the causal interpretation is not, which is the precise condition that motivates moving the question to a different unit and a different design.

### 3.1.3 The self-selection threat, isolated

The reason the article-level evidence cannot be read causally has a name, and the literature has converged on it. Self-selection, sometimes split into a quality-bias component and an early-view component, is the proposition that authors choose to make their better work open, or that better-resourced and more-cited authors are disproportionately likely to publish open, so that the measured advantage reflects the pre-existing quality and resources of the article rather than any effect of access. Stevan Harnad [\[110\]](#ref-110), in a methodological critique of an influential null-leaning study by Davis, argued that the way open access is operationalized, in particular whether free self-archiving is counted as open or non-open, materially changes the estimated advantage, and that confirmation bias and inconsistent operationalization run in both directions. Ottaviani [\[87\]](#ref-87) addressed the self-selection problem directly by studying post-embargo articles, where the access status changes by a calendar rule rather than by author choice, and reported that a modest advantage of as much as 19 percent survives even when articles are embargoed during their prime citation years, while also confirming a rich-get-richer pattern in which already-advantaged articles benefit most. Dorta-Gonzalez and colleagues [\[88\]](#ref-88) invoked the early-view and selection-bias postulates explicitly as the two competing explanations in a longitudinal, multidisciplinary analysis across all Web of Science subject categories from 2009 to 2014, and Basson and colleagues [\[43\]](#ref-43) used the open-access labels newly introduced into Web of Science metadata to compare Directory of Open Access Journals articles against subscription articles for which no self-archived version exists, a design constructed to reduce the self-archiving confound.

The mechanism here must be stated precisely, because the design of this dissertation depends on it. The self-selection threat is not a measurement error; it is a confounding pathway. The driver is unobserved article or author quality. The mechanism is that quality raises both the probability of being made open, through author choice and funder resources, and the probability of being cited, through the ordinary process by which better work is cited more. The observable effect is a positive association between openness and citation. The operational consequence is that an estimator which compares open to non-open articles will attribute to access an effect that belongs to quality, producing an upward-biased coefficient. The strategic implication is that breaking this confound requires a setting in which the assignment of openness is not made by the author and is not a function of article quality. Two strategies appear in the literature: mandates, which move the openness decision from the author to the institution or funder, reviewed in Section 3.4; and within-journal or post-embargo designs, which hold the outlet constant and change access by rule. This dissertation adopts a third and stronger strategy, a policy event at the level of the data producer, which is reviewed as a natural experiment in Section 3.5 and developed as a design in Chapter 5.

A second confounding pathway, distinct from quality self-selection and frequently conflated with it, deserves separate treatment because it bears directly on how the dissertation interprets the timing of its event-study path. This is the early-view or early-access channel. The proposition, raised explicitly as one of the two competing postulates by Dorta-Gonzalez and colleagues [\[88\]](#ref-88) and discussed in the early reviews [\[2\]](#ref-2), [\[94\]](#ref-94)], is that open articles are available sooner, often as preprints or immediately on acceptance, and that earlier availability mechanically advances the accrual of citations without any change in the ultimate citation total. The driver is the timing of availability; the mechanism is that citations accumulate over calendar time and earlier availability shifts the accrual curve left; the observable effect is a measured advantage concentrated in the early post-publication window that shrinks as the closed-access comparison articles catch up; the operational consequence is that a study which measures citations in a short window after publication will overstate the durable advantage. The relevance to this dissertation is twofold. First, the early-view channel is an article-level phenomenon that does not transpose cleanly to the mission level, because a mission's data do not have a single publication date whose timing can be advanced; the treatment is a standing change in access, not a one-time earlier release of a single object. Second, the dissertation's event-study specification, which traces a dynamic path over event time rather than a single short-window difference, is the instrument that distinguishes a durable level or slope change from a transient early-view bump that decays. A genuine access-cost effect of the kind North predicts should build and persist as the user community discovers and adopts the now-cheaper data, whereas a pure early-view artifact would appear as a spike that fades, and the lag structure of the event study is what tells them apart. This is a concrete instance of how reading the article-level literature's confounders informs the mission-level design rather than merely cataloguing threats.

Confidence at the close of Section 3.1 is calibrated as follows. The existence of an open-access citation advantage as an association is supported at high confidence by a deep and replicated literature [\[32\]](#ref-32), [\[48\]](#ref-48), [\[66\]](#ref-66), [\[123\]](#ref-123), [\[148\]](#ref-148)]. The proposition that the association is partly or wholly an artifact of self-selection is supported at moderate-to-high confidence by the systematic-review and critique literature [\[7\]](#ref-7), [\[63\]](#ref-63), [\[94\]](#ref-94), [\[110\]](#ref-110)]. The proposition that a residual, genuinely causal advantage survives careful design is supported at moderate confidence by the post-embargo and label-based studies [\[43\]](#ref-43), [\[87\]](#ref-87)]. What would raise confidence in the causal reading is exactly what is missing: a design in which openness is assigned by policy rather than chosen by authors. That observation is the hinge of the entire chapter.

**Table 3.1. Representative open-access citation-advantage studies: design, finding, and limitation.**

| Study | Unit and sample | Design | Direction of finding | Principal limitation for causal reading |
|---|---|---|---|---|
| Eysenbach [\[32\]](#ref-32) | Articles in *PNAS* | Within-journal OA vs non-OA | Positive, large early | Author self-selection into OA |
| Lifang et al. [\[66\]](#ref-66) | 12,354 articles, 93 Oxford Open journals | Cross-sectional comparison | Positive overall, negative in humanities | Field confounding; selection |
| Xianwen et al. [\[123\]](#ref-123) | 1,761 *Nature Communications* articles | OA vs non-OA, citations plus usage | Positive, sustained downloads | Single high-prestige venue; selection |
| Ottaviani [\[87\]](#ref-87) | Post-embargo articles | Calendar-rule access change | Positive but modest (~19%), rich-get-richer | Residual selection; embargo windows vary |
| Basson et al. [\[43\]](#ref-43) | WoS 2013-2015, DOAJ vs subscription | Multiple measures, OA labels | Mixed by subject area | Excludes self-archived; coverage of labels |
| Davis and Walters [\[94\]](#ref-94) | Review | Critical literature review | Downloads up, citations equivocal | Inherits primary-study weaknesses |
| Langham-Putrow et al. [\[63\]](#ref-63) | Systematic review | Protocol-driven synthesis | Majority positive, magnitude contested | Selection pervasive; heterogeneity large |
| Plume [\[7\]](#ref-7) | Commentary | Synthesis | Advantage unproven | No new identification |

## 3.2 The open-data and dataset-reuse citation advantage

### 3.2.1 The foundational dataset-level finding

The dissertation's outcome is downstream use of mission data, so the more proximate literature is the one on open data and dataset reuse rather than on open articles. The foundational study is Piwowar and Vision [\[96\]](#ref-96), the closest article-level analogue to the question this dissertation asks at the mission level. Piwowar and Vision examined whether studies that make their underlying data publicly available accrue more citations, and reported a data-reuse and open-data citation advantage: papers with publicly available data were cited more, and the authors traced reuse by identifying third-party papers that used the shared data, which begins to isolate genuine reuse from mere association. The underlying dataset of that study is itself deposited and citable [\[39\]](#ref-39), a fact that is more than a curiosity: it makes the Piwowar and Vision result an instance of the very practice it studies and an early model of the reproducibility stance this dissertation adopts. The method, linking shared datasets to downstream citing papers, is the linkage logic this dissertation must operationalize at the mission level, and its limitation, the difficulty of fully separating data-sharing from the quality and openness of the sharing authors, is the self-selection problem of Section 3.1 transposed to data.

Colavizza and colleagues [\[19\]](#ref-19) extended the dataset-level finding to a much larger corpus, analyzing more than half a million articles and finding that articles linking to deposited research data accrued more citations, with the advantage holding across several journals and fields. The contribution of Colavizza and colleagues is scale and the use of explicit data-availability statements as the treatment marker, a more reproducible operationalization than ad hoc detection of data sharing. Its limitation is again selection: articles that include a data-availability statement and a deposit may differ systematically from those that do not, in ways correlated with citability. Read carefully, the dataset-level advantage is real as an association, attested by two independent studies of very different scale [\[19\]](#ref-19), [\[96\]](#ref-96)], made credible by the consistency of sign and by the partial isolation of reuse, bounded by the same selection caveat that governs the open-access literature, and open to challenge only on the possibility that data-sharing authors are systematically different. Confidence in the dataset-level association is high; confidence in its causal reading at the article level is low, for the identical reason as in Section 3.1.

It is worth dwelling on why the dataset-level literature, despite sharing the selection problem, is the more apt precedent for this dissertation than the article-level open-access literature. The open-access literature treats the citing object, the article, as both the treated unit and the cited unit, which fuses the access decision and the quality of the cited work into a single object. The dataset-level literature begins to separate them: the treated object is the dataset, and the outcome is the behavior of a different set of objects, the downstream papers that reuse the data. This separation is the structure the dissertation scales up, in which the treated object is the mission, the access decision is the mission's release policy, and the outcome is the behavior of the population of downstream papers and dataset citations produced by non-team researchers. Piwowar and Vision's traced-reuse method [\[96\]](#ref-96), identifying the third-party papers that actually used the shared data rather than inferring reuse from a data-availability flag, is the article-level prototype of the bibliographic-linkage rule the dissertation operationalizes in Chapter 4 through mission, instrument, dataset-identifier, and acknowledgment-text matching. The persistence of that traced dataset as a citable object [\[39\]](#ref-39) is not incidental: it embodies the reproducibility commitment the dissertation makes, namely that the evidence for or against H1 should be as accessible and reusable as the mission data whose openness is under test, and it demonstrates that data citation as a first-class practice was feasible even in 2013, which bounds how far back the dataset-citation outcome can plausibly reach.

### 3.2.2 Reuse behavior and its measurement
Beyond the headline advantage, a literature documents how data are actually reused, which matters because this dissertation's publication-rate outcome is a count of reuse. Fu and colleagues [\[71\]](#ref-71) analyzed scientific-dataset reuse behavior in the open-access literature of PubMed Central, characterizing the dimensions along which researchers reuse datasets and the citation status of high-reuse datasets, and tying reuse to questions of intellectual property in data sharing. Krahe and colleagues [\[73\]](#ref-73) conducted a scientometric review of 95 publications on health-data sharing for secondary use, using co-citation and keyword co-occurrence to map the thematic structure of the reuse field and to identify the social-licence and governance concerns that condition reuse. Lodwick [\[61\]](#ref-61) examined data sharing, citation, and reuse in archaeobotany, a data-rich sub-discipline, reviewing 239 articles across 16 journals and documenting both the forms of data shared and the patterns of data citation in meta-analyses. This case shows, at fine grain, how reuse and citation diverge within a single field. Haya and colleagues [\[38\]](#ref-38) traced a decade of open-data practice at the University of Edinburgh and framed the change around the FAIR principles and a 2021 institutional open-research policy, which previews the policy-event logic of Section 3.4.

These studies share a method, bibliometric and scientometric analysis of reuse, and a limitation: they describe reuse where it occurs rather than estimate the effect of openness on the quantity of reuse. They relate to the gap by supplying the construct, downstream reuse, that the dissertation's publication-rate outcome operationalizes, and they warn that reuse is heterogeneous across fields and entangled with governance and intellectual-property considerations. The mechanism they collectively support is that lowering the cost of obtaining a dataset raises the probability that a non-producing researcher will reuse it. Their descriptive design cannot rule out that high-reuse datasets were simply more valuable to begin with. This is the data-side statement of the same correlation-versus-causation problem, and it is downgraded to a descriptive, moderate-confidence reading accordingly.

### 3.2.3 Data citation as practice: whether the dataset-citation outcome is even measurable

The dissertation specifies a second outcome, the rate of formal citations to a mission's datasets as first-class objects. Whether that outcome can be measured at all is governed by a literature on data-citation practice, and that literature delivers a sobering, design-relevant verdict: formal data citation is sparse, inconsistent, and recent, which is exactly why the shared bible restricts the dataset-citation outcome to the later window with explicit power caveats. Park, You, and Wolfram [\[42\]](#ref-42) examined the prevalence of data citation in biomedical full-text articles and found that informal data citation, in which data are mentioned and acknowledged in the body text rather than in the reference list, is far more common than formal data citation, in which the dataset appears alongside bibliographic references. This finding is foundational for the dissertation's measurement strategy: it implies that any count restricted to formal reference-list data citations will sharply undercount real reuse, and that acknowledgment-text matching, which the dissertation's frozen linkage rule includes, is necessary to capture the informal majority.

Gregory and colleagues [\[57\]](#ref-57) reported the largest known survey of data-citation practices, with 2,492 respondents drawn representatively by discipline from Web of Science authors, and documented both wide disciplinary variation in whether and how researchers cite data and the motivations behind citing or not citing. The method, a representative survey rather than a bibliometric extraction, complements the extraction-based studies and reinforces their conclusion: data-citation practice is not yet standardized, and disciplinary norms dominate. The institutional and standards literature attempts to remedy this. Helena Cousijn and colleagues [\[40\]](#ref-40) produced a practical data-citation roadmap for publishers aligned to the Joint Declaration of Data Citation Principles, structured around the life of a paper, and Federer [\[67\]](#ref-67) reported 68 specific recommendations from a FORCE11 workshop on measuring and mapping data reuse. Both document that the infrastructure for formal data citation was still being assembled in the late 2010s. The relation to the gap is twofold. First, these studies justify, on the basis of evidence rather than assertion, the dissertation's decision to treat the dataset-citation outcome as available only in the later window and to report it with explicit power caveats. Second, they justify the frozen-linkage-rule strategy, because a measurement instrument that changes as data-citation norms mature would confound a change in counting with a change in output, which is the Kuznets relabeling threat that Chapter 4 operationalizes.

**Table 3.2. Open-data, reuse, and data-citation-practice literature and its bearing on the design.**

| Study | Focus | Method | Key finding | Bearing on the design |
|---|---|---|---|---|
| Piwowar and Vision [\[96\]](#ref-96) | Open-data citation advantage | Link shared data to citing papers | Data-available papers cited more; reuse traced | Article-level analogue to the mission-level question |
| Colavizza et al. [\[19\]](#ref-19) | Data-link citation advantage | >500k articles, availability statements | Positive advantage at scale | Confirms association; selection unresolved |
| Fu et al. [\[71\]](#ref-71) | Dataset reuse behavior | Bibliometric, PubMed Central | Reuse multidimensional; high-reuse datasets identified | Construct for the publication-rate outcome |
| Park et al. [\[42\]](#ref-42) | Data-citation prevalence | Text extraction, biomedical | Informal citation far exceeds formal | Justifies acknowledgment-text matching |
| Gregory et al. [\[57\]](#ref-57) | Data-citation practice | Survey, n=2,492 | Wide disciplinary variation | Justifies later-window-only dataset-citation outcome |
| Cousijn et al. [\[40\]](#ref-40) | Publisher roadmap | Standards synthesis | Formal data citation still being built | Explains sparse early formal citation |
| Federer [\[67\]](#ref-67) | Reuse metrics | Workshop synthesis, 68 recs | Standards not yet adopted | Power caveat for dataset-citation arm |

## 3.3 Field, funding, and topic heterogeneity of the advantage

### 3.3.1 Why heterogeneity is the central empirical fact, not a nuisance

A naive reading of Sections 3.1 and 3.2 would extract a single number, the open-access or open-data citation advantage, and treat the dispersion around it as noise. The heterogeneity literature establishes the opposite: the dispersion is the signal. The size, and even the sign, of the advantage depends on field, on funding, and on topic. That dependence is why a single pooled article-level estimate is uninformative for policy and why the dissertation's design estimates and reports sensor-class heterogeneity rather than averaging it away. The advantage is heterogeneous in a structured, not random, way, and a set of studies finds that it varies systematically with measurable covariates. When an effect's sign flips across subgroups, a pooled mean is a weighted average of opposing effects and is not a meaningful summary of any of them. The same logic, transposed to treatment timing, motivates the Callaway and Sant'Anna estimator in the methodological anchor. The heterogeneity literature is itself associational and shares the selection problem, so some apparent heterogeneity could reflect differential selection across fields rather than a differential causal effect, which the literature largely cannot resolve.

### 3.3.2 Field and discipline

The clearest evidence of field heterogeneity comes from the multidisciplinary, all-category studies. Dorta-Gonzalez and colleagues [\[88\]](#ref-88) analyzed gold open access across every subject category in Web of Science from 2009 to 2014 and found that the citation advantage was not consistent across fields, with the early-view and selection-bias postulates offered as competing explanations for where it appeared. The companion journal-level analysis across the 27 subject areas of Scopus [\[89\]](#ref-89), [\[91\]](#ref-91)] reinforced the conclusion that prevalence and advantage of gold open access differ markedly across research areas, and added the methodological point that a journal-level approach yields different results from an article-level one. Basson and colleagues [\[43\]](#ref-43) found mixed results across Web of Science subject areas using three distinct citation-advantage measures, and emphasized that the conclusion one reaches depends on which measure is used, a methodological caution this dissertation absorbs by specifying its outcome construction in advance and cross-checking across two databases. Lifang and colleagues [\[66\]](#ref-66), as already noted, found a negative advantage in humanities Oxford Open journals, the sharpest single demonstration that the sign is not universal. Nishikawa and Murakami [\[56\]](#ref-56) added a structural dimension by decomposing the advantage into within-discipline and interdisciplinary citation components, finding that gold open access increased both in many fields but only interdisciplinary citations in chemistry, computer science, and clinical medicine. The mechanism this suggests is that openness lowers the access cost most for distant users, who are precisely the interdisciplinary citers, a fine-grained, mechanism-named instance of the access-cost logic that North supplies as the dissertation's anchor.

### 3.3.3 Funding and topic

Funding is a confounder and a moderator at once. Dorta-Gonzalez and Dorta-Gonzalez [\[92\]](#ref-92) tested the funding hypothesis directly on more than 128,000 research articles across 40 subject categories from 2016, of which 31 percent were funded, and found that funding affects both the publication modality, because funders mandate open access, and the citations received, because well-funded studies are cited more. This is the funding channel of the self-selection problem stated as a measured fact: funder mandates and funder resources jointly produce a spurious component of the open-access advantage. The design implication is direct, and the dissertation acts on it: any credible estimate must hold funding-correlated quality constant, which at the mission level is partly addressed by matching on sensor class and mission age and by the no-prior-affiliation specification. Topic heterogeneity is documented by Sotudeh [\[37\]](#ref-37), who used a matched-pairs design across 47 Elsevier journals and natural-language-processing matching on title and abstract content to ask whether the advantage depends on paper topic, and found that it does, with authors plausibly selecting citation-attractive topics for open outlets. Sotudeh and Estakhr [\[36\]](#ref-36) examined the sustainability of the advantage over time in Elsevier's author-pays hybrid journals, asking whether the advantage persists or decays, which is the temporal-dynamics question that, at the mission level, becomes the event-study lag path. The cross-country dimension is supplied by Hadad, Raban, and Aharony [\[106\]](#ref-106), who compared open-access publication and citation trends in Austria, Israel, and Mexico from 2010 to 2020 using Scopus and a weighted open-access citation-impact index, finding that national policy and infrastructure shape the patterns, and by their longitudinal policy assessment [\[105\]](#ref-105), which links the impact of open-access publications to the policy environment over time.

The synthesis of Section 3.3 is that the advantage is a distribution, not a point, and that the distribution is organized by field, funding, and topic, each of which is also a selection channel. The relation to the gap is that this heterogeneity is fatal to a pooled article-level policy estimate and is the substantive reason the dissertation estimates heterogeneity by sensor class as a primary, reported quantity rather than a robustness afterthought. Confidence that the advantage is structurally heterogeneous is high; confidence that the heterogeneity reflects differential causal effects rather than differential selection is moderate, and the design responds by estimating heterogeneity within an identification strategy rather than from raw comparisons.

## 3.4 Policy- and mandate-level evidence: what changes when openness is imposed

### 3.4.1 The mandate as the first break in the self-selection problem

The single most important methodological move available at the article level for breaking self-selection is to study openness that is mandated rather than chosen, because a mandate transfers the openness decision from the author, whose choice is correlated with quality, to an institution or funder, whose rule is not. Gargouri and colleagues [\[34\]](#ref-34) executed this move and produced the most identification-conscious study in the article-level corpus. They compared self-selected open access against mandated open access and found that open access increases citation impact under both, but that the effect persists under mandate, where author self-selection is removed by construction, and is larger for higher-quality research. The method, exploiting an institutional mandate as a quasi-experimental assignment, is the article-level precursor of the policy-event design this dissertation builds at the mission level. The finding that the effect survives the removal of self-selection is the strongest single piece of evidence in the corpus that a genuine, non-spurious access effect exists. Its limitation is that a mandate is not random; institutions that adopt mandates may differ from those that do not, and the comparison is still between articles rather than between data producers. Its relation to the gap is that it points directly at the design this dissertation adopts and shows that the design logic is sound while leaving the unit-of-analysis gap, article versus mission, wide open.

### 3.4.2 The benefits-of-openness and policy-framework literature

A complementary literature documents the benefits of open practices for researchers and the policy frameworks that govern openness, which matters because the dissertation's treatment is a policy. McKiernan and colleagues [\[75\]](#ref-75) surveyed how open practices, including open access, open data, and open code, help researchers succeed, assembling the evidence that openness is associated with increased citation, media attention, and collaboration, and framing openness as a career-rational choice. The contribution is a synthesis of the incentive structure that openness creates; the limitation is that it synthesizes largely associational evidence and is explicitly advocacy-adjacent, so its claims are read as motivating priors rather than as identified effects. The policy-framework literature is represented by Kuchma [\[44\]](#ref-44), who provided an overview of the growth of open-access, open-data, and open-science policies and a roadmap for their adoption, and by Pascu and Burgelman [\[21\]](#ref-21), who positioned open data as the building block of twenty-first-century open science and connected it explicitly to the FAIR principles of findability, accessibility, interoperability, and reusability. These FAIR-anchored treatments matter because they supply the construct the dissertation uses to distinguish nominal from functional openness: a mission coded as open in license but functionally encumbered has not lowered the relevant transaction cost, and the FAIR vocabulary is what makes that distinction operational.

The governance literature adds a necessary caution. Carroll and colleagues [\[108\]](#ref-108), [\[109\]](#ref-109)] developed and operationalized the CARE principles for Indigenous data governance, Collective Benefit, Authority to Control, Responsibility, and Ethics, alongside FAIR, documenting that open is not an unqualified good and that some data carry rights and interests that constrain openness. Grecu [\[72\]](#ref-72) examined the challenges of open-scientific-data-policy development in a developing-country context, the Republic of Moldova, showing that the capacity to implement open-data policy is unevenly distributed. These studies do not bear directly on the citation-yield mechanism, but they bound the external-validity claim: the access-cost mechanism the dissertation tests operates where the only obstacle to use is access cost, and the CARE and capacity literatures identify settings where other obstacles dominate. The relation to the gap is that they sharpen, rather than fill, it: they confirm that openness is a policy variable with real heterogeneity in how it is implemented and what it means, which is why the dissertation must code functional, not merely nominal, openness.

### 3.4.3 Difference-in-differences applied to openness, at the article level

One study in the corpus applies the dissertation's own estimator family to the openness question, and it is instructive precisely because of how far short of the mission-level design it falls. Wei and Zhao [\[118\]](#ref-118) used a difference-in-differences framework to study 60 journals that reverse-flipped from open access back to subscription, exploiting the switch to detect the effect of access model on citation impact while avoiding the problem that ordinary flips leave no subscription comparison articles. The method is the closest article-level precedent to this dissertation's design: a policy-like switch, a difference-in-differences estimator, and an explicit attempt to construct a valid comparison. The finding contributes evidence on the switching mechanism rather than the static cross-section. The limitation, and the reason it does not close the gap, is that the unit is the journal article and the treatment is a publisher's business-model decision, not a data producer's release policy, and the design is a two-period before-after DiD rather than a staggered, heterogeneity-robust event study with matched controls. Wei and Zhao thus demonstrate the feasibility and the value of a DiD approach to openness while leaving every distinctive feature of the mission-level problem, the unit, the staggered timing, the sensor-class heterogeneity, and the distribution-log mechanism check, unaddressed. This is the cleanest single illustration that the methodological gap and the unit-of-analysis gap are real and joint.

**Table 3.3. Policy- and mandate-level evidence: how each begins, but does not complete, the move to identification.**

| Study | Treatment studied | Design feature that breaks selection | What it still leaves to the gap |
|---|---|---|---|
| Gargouri et al. [\[34\]](#ref-34) | Mandated vs self-selected OA | Mandate removes author choice | Article unit; mandate non-random |
| Wei and Zhao [\[118\]](#ref-118) | Journal reverse-flip OA to subscription | DiD on a policy-like switch | Article/journal unit; two-period, no matching |
| McKiernan et al. [\[75\]](#ref-75) | Open practices generally | None (synthesis) | Associational; advocacy-adjacent |
| Kuchma [\[44\]](#ref-44) | OA/OD policy frameworks | None (roadmap) | Descriptive; no effect estimate |
| Pascu and Burgelman [\[21\]](#ref-21) | Open data and FAIR | None (framework) | Supplies construct, not estimate |
| Carroll et al. [\[108\]](#ref-108), [\[109\]](#ref-109)] | CARE governance | None (governance) | Bounds external validity |
## 3.5 The mission-level natural experiment: Landsat and Copernicus as program-level evidence

### 3.5.1 Landsat 2008 as the design precedent

The literature that comes closest to the dissertation's unit of analysis is the remote-sensing work on the Landsat program's 2008 transition to free-and-open data. This is the design precedent, and it serves as the pivot of the chapter. It shows that the access-cost mechanism operates at the level of a data producer and produces a structural change in downstream use. By its own methodological limits it also shows exactly why a single before-after program narrative cannot identify a causal effect and must be embedded in a multi-mission design. Wulder and colleagues [\[122\]](#ref-122) documented the status of the Landsat program and the benefits of the free-and-open data policy, reporting that the 2008 policy change was followed by a rise in scene distribution from the order of tens of thousands of scenes per year to tens of millions, and by a sharp expansion in scientific publications and operational products. Zhu and colleagues [\[132\]](#ref-132) corroborated the program-level effect in a companion paper devoted to the benefits of the free-and-open Landsat data policy. Wulder and colleagues [\[77\]](#ref-77), reviewing fifty years of Landsat science and impacts, characterized the 2008 free-and-open decision as unprecedented for medium-resolution Earth observation and as the proximate cause of a proliferation of science and application opportunities.

The mechanism in the Landsat episode is named precisely and maps onto the dissertation's causal chain. The driver is the institutional rule change, the 2008 decision to make all past and future Landsat data free and open. The mechanism is that the transaction cost of obtaining a scene fell from a per-scene fee and an ordering process to the cost of a download. The observable effect, documented in two stages, is first a roughly three-orders-of-magnitude rise in distribution, the upstream usage measure, and then an expansion in publications and operational products, the downstream measure. The operational consequence is the documented proliferation of time-series and continuous-monitoring methods that were previously too costly to attempt. The strategic implication, for this dissertation, is that the same mechanism, observed once with a single program and no control, can be generalized into an identified estimate if it can be observed across many missions with staggered timing and matched comparison missions. The bibliometric corroboration is independent: a systematic review of fifty years of Landsat change-detection studies [\[82\]](#ref-82) reported that the average number of Landsat images used per study rose from about 10 before 2008 to about 100,000 by 2020, with the 2008 archive opening evident in the literature as a turning point, a quantified, publication-side signature of the policy change drawn from Web of Science and Scopus. NTRS grey literature [\[135\]](#ref-135)] describes the same 2008 shift as a paradigm change from analyzing individual images to continuous temporal monitoring, which is the qualitative mechanism behind the quantitative break.

The continuous-monitoring methods that the Landsat opening enabled are themselves evidence of the mechanism, because they could not have existed under the prior fee-based regime. Before 2008, the per-scene cost confined most analyses to a handful of images, which is why the dominant methods were single-image or bi-temporal change detection [\[22\]](#ref-22), [\[26\]](#ref-26)]. After 2008, the marginal cost of an additional scene fell to nearly zero, and the methods that became feasible, dense time-series reconstruction, annual gap-free surface-reflectance compositing, and continuous land-cover monitoring [\[16\]](#ref-16), [\[29\]](#ref-29)], are exactly the methods that consume thousands or millions of scenes per study. This is a direct, observable consequence of the transaction-cost change: the access cost did not merely raise the count of conventional studies, it changed the production function of remote-sensing science by making data-intensive methods economically possible. The point sharpens the dissertation's argument; it shows that the access-cost reduction operated at the level of what research was feasible at all, not only at the level of how many researchers chose to do feasible work. It also cautions that the publication-count outcome, taken alone, understates the change, because a single post-2008 time-series paper can embody a quantity of data use that would have required hundreds of pre-2008 papers, which is part of why the dissertation pairs the publication-rate outcome with the distribution-volume outcome rather than relying on counts alone.

The Landsat precedent carries the load-bearing argument of the chapter. Mission-level open-data policy can cause a large change in downstream scientific use: the distribution and publication breaks following the 2008 policy [\[77\]](#ref-77), [\[122\]](#ref-122), [\[132\]](#ref-132)] and the independent bibliometric quantification of the images-per-study break [\[82\]](#ref-82) all date a sharp change in usage to a sharp change in access policy, and that policy plausibly lowered the relevant transaction cost, exactly the signature a causal effect operating through that cost would leave. The convergence of upstream distribution evidence, downstream publication evidence, and qualitative method-shift evidence is harder to reconcile with a pure-coincidence account than any single strand would be. One limit is decisive and must be protected: this is a single program observed before and after a single date with no contemporaneous control, so the evidence identifies an association in time, not a causal effect. Secular trends in computing, data availability, and the maturation of the remote-sensing community could produce part or all of the break. The early 2000s and 2010s saw large secular increases in computational capacity and in remote-sensing research generally, so a single-program before-after cannot attribute the break to the policy. Meeting that objection is the dissertation's entire contribution: embed the Landsat-type episode in a matched, staggered, multi-mission design with not-yet-treated comparison missions, so that the secular trend is absorbed by the comparison group and the policy effect is identified by the difference in differences. Confidence that the Landsat episode demonstrates a strong mechanism is high; confidence that it identifies a causal magnitude on its own is low, and the gap between those two confidence levels is the space the dissertation occupies.

### 3.5.2 Copernicus uptake as a second program-level case

Landsat is not the only program-level case. The European Copernicus programme provides a second, partly independent instance of free-and-open Earth-observation data and of the user-uptake dynamics that follow. Apicella, De Martino, and Quarati [\[68\]](#ref-68) studied Copernicus user uptake from data to applications, documenting the initiatives undertaken to increase awareness and competence, the bibliographic analysis of downstream applications, and recommendations to improve uptake. The contribution is a second free-and-open program in which downstream use is studied as the outcome of deliberate uptake effort, which is informative about the mechanism by which open data converts to applications. The limitation, for the dissertation's purposes, is that the Copernicus literature is largely descriptive and uptake-focused rather than identification-focused, and it does not provide a before-after policy switch comparable to Landsat 2008 because Copernicus Sentinel data were free and open from the outset. Its relation to the gap is that it widens the evidence that the mechanism is general across programs and instruments while showing that the literature still lacks the comparative, staggered design that would turn these program narratives into an estimate. The broader Earth-observation value literature, including the biodiversity-conservation case for free and open satellite data [\[121\]](#ref-121), reinforces that the socioeconomic and scientific stakes of the open-data decision are first-order, which establishes the materiality of the problem, but it too is argued by demonstration rather than by identification.

### 3.5.3 The materiality of the mission-level question

The argument requires that the problem be not only real but material. The Landsat and Copernicus literatures establish materiality at the level of magnitude. The distribution change documented for Landsat was an order-of-magnitude phenomenon, not a marginal one [\[77\]](#ref-77), [\[122\]](#ref-122)]; the images-per-study change was three to four orders of magnitude [\[82\]](#ref-82); the downstream applications span land cover, agriculture, fire, coastal monitoring, and biodiversity conservation [\[68\]](#ref-68), [\[121\]](#ref-121)]. Materiality is therefore well supported by the size of the documented changes, bounded by the single-program identification limit, and open to challenge only on the possibility that the magnitude is secular rather than policy-driven, which is the same objection as in 3.5.1 and is answered by the same design. Confidence in materiality is high; the magnitude of the effect that is specifically attributable to policy, as opposed to secular trend, is exactly the quantity the dissertation is designed to estimate and is not claimed here.

**Table 3.4. Program-level natural-experiment evidence and its identification limit.**

| Study | Program and event | Documented break | Identification status |
|---|---|---|---|
| Wulder et al. [\[122\]](#ref-122) | Landsat, 2008 free-and-open | Distribution from ~10^4 to ~10^7 scenes/yr; publications expand | Single program, no control |
| Zhu et al. [\[132\]](#ref-132) | Landsat, 2008 | Corroborates program-level benefits | Single program, no control |
| Wulder et al. [\[77\]](#ref-77) | Landsat, 50-yr review | 2008 unprecedented; proliferation of science | Narrative, no control |
| Hemati et al. [\[82\]](#ref-82) | Landsat change-detection | Images/study ~10 (pre-2008) to ~10^5 (2020) | Bibliometric, no contemporaneous control |
| Apicella et al. [\[68\]](#ref-68) | Copernicus uptake | Downstream applications grow with uptake effort | Descriptive; open from outset |
| Turner et al. [\[121\]](#ref-121) | Free/open EO for biodiversity | Conservation value of open data | Argument by demonstration |

## 3.6 Synthesis: the two gaps and the propositions that follow

### 3.6.1 The first gap: unit of analysis

The literature reviewed in Sections 3.1 through 3.4 is, with the single partial exception of Wei and Zhao [\[118\]](#ref-118), measured at the level of the individual article or dataset. The treatment in that literature is an author's or a publisher's decision to make a particular output open. The unit that NASA and the Jet Propulsion Laboratory actually fund and operate, and the unit at which the policy lever is actually pulled, is the mission. No study in the assembled corpus treats the mission as the unit of analysis and the mission's transition to free-and-open release as the treatment. This is the unit-of-analysis gap. It is not a corpus weakness to be remedied by a further sweep; it is, as the evidence-gap register in the expansion plan records, the deliberate gap the dissertation exists to fill, because none of the article-level studies can speak to the policy question that NASA faces, which is whether and when to make a mission's data open and how much to invest in the data systems that support open release. The Landsat and Copernicus literatures [\[68\]](#ref-68), [\[77\]](#ref-77), [\[122\]](#ref-122), [\[132\]](#ref-132)] come closest to the mission unit, but they describe single programs without contemporaneous controls and therefore cannot generalize the mechanism into an estimate.

### 3.6.2 The second gap: identification

The second gap is that the article-level and dataset-level evidence is overwhelmingly associational and is vulnerable to selection, as the systematic-review literature establishes at high confidence [\[7\]](#ref-7), [\[63\]](#ref-63), [\[94\]](#ref-94)] and as the mechanism analysis of Section 3.1.3 makes precise. The mandate literature [\[34\]](#ref-34) and the post-embargo and label-based designs [\[43\]](#ref-43), [\[87\]](#ref-87)] partially break selection and are the strongest evidence that a genuine access effect exists, but they remain at the article level and the mandate is not random. The one difference-in-differences study [\[118\]](#ref-118) is two-period, unmatched, and at the journal-article level. No study combines a policy-event treatment, a heterogeneity-robust staggered estimator, matched comparison units, and a producer-level unit of analysis. This is the identification gap, and it is what modern difference-in-differences methods, applied to the staggered timing of open-data adoption across NASA Earth missions, can close in a way the existing literature cannot.

The two gaps are joint, and their jointness is the contribution. Closing the unit gap without the identification gap would yield more single-program narratives. Closing the identification gap without the unit gap would yield another article-level study. Closing both at once, by treating the mission as the unit and the mission's open-data adoption as a staggered policy event analyzed with matched, heterogeneity-robust difference-in-differences, is what no work in the corpus does and what the design in Chapters 5 and 6 specifies. The Kuznets measurement discipline supplies the final element the literature underweights: the dataset-citation-practice studies [\[40\]](#ref-40), [\[42\]](#ref-42), [\[57\]](#ref-57), [\[67\]](#ref-67)] show that the outcome is a constructed proxy whose counting conventions change over time, so a credible design must freeze the counting rule across periods and use distribution logs as an independent mechanism check, separating real new output from improved counting in a way the descriptive reuse literature [\[61\]](#ref-61), [\[71\]](#ref-71), [\[73\]](#ref-73)] does not attempt.

### 3.6.3 The propositions that follow

From the synthesis, the following propositions are stated. They are not the dissertation's hypotheses, which are fixed verbatim in the shared bible as H0 and H1 and are restated in Chapter 1; they are the literature-derived propositions that justify the design and that the hypotheses operationalize.

Proposition 1, on the mechanism. Free-and-open data release lowers the transaction cost of obtaining and reusing a mission's data, and lowering that cost should raise impersonal downstream use by researchers who were not part of the mission team. This proposition rests on the North institutional mechanism [\[85\]](#ref-85) and is supported as an association by the entire open-data literature [\[19\]](#ref-19), [\[96\]](#ref-96)] and as a producer-level phenomenon by the Landsat episode [\[77\]](#ref-77), [\[122\]](#ref-122), [\[132\]](#ref-132)]. Confidence in the mechanism is moderate-to-high; confidence in its magnitude at the mission level is not yet established and is the object of estimation.

Proposition 2, on the ordering of responses. Because distribution is upstream of publication, a genuine access-cost effect should appear first in distribution volume and only later in publications and, later still and more weakly, in formal dataset citation. This proposition rests on the Landsat ordering, distribution rising before publications [\[77\]](#ref-77), [\[122\]](#ref-122)], and on the data-citation-practice finding that formal citation is sparse and lagging [\[42\]](#ref-42), [\[57\]](#ref-57)]. It generates the dissertation's use of distribution logs as both an early-response outcome and a relabeling check: a publication rise unaccompanied by a distribution rise would, under the Kuznets discipline, indicate counting rather than new use.

Proposition 3, on heterogeneity. The effect of open release is structurally heterogeneous and should be larger where the latent user community is large and held back only by access cost, and smaller where the binding constraint is analysis capacity or community size. This proposition rests on the field, funding, and topic heterogeneity literature [\[37\]](#ref-37), [\[56\]](#ref-56), [\[88\]](#ref-88), [\[91\]](#ref-91), [\[92\]](#ref-92), [\[106\]](#ref-106)] and on the Landsat-versus-other-sensor contrast implied by the optical-imaging concentration of the documented effect [\[122\]](#ref-122). It justifies estimating and reporting sensor-class heterogeneity as a primary quantity.

Proposition 4, on identification. A credible estimate of the mission-level effect requires a design that does not assume open and restricted missions are otherwise identical and that does not rely on a single before-after comparison. This proposition rests on the selection critique [\[34\]](#ref-34), [\[63\]](#ref-63), [\[110\]](#ref-110)] and on the single-program identification limit of the Landsat literature [\[77\]](#ref-77), [\[122\]](#ref-122)], and it points directly to a matched, staggered difference-in-differences event study with not-yet-treated comparison missions, which is the design Chapter 5 develops.

Proposition 5, on measurement. The outcome is a constructed proxy whose counting conventions evolve, so the linkage rule must be frozen across periods and the result must be reported as a sensitivity region rather than a point. This proposition rests on the data-citation-practice literature [\[40\]](#ref-40), [\[42\]](#ref-42), [\[57\]](#ref-57), [\[67\]](#ref-67)] and on the Kuznets-lineage measurement discipline [\[62\]](#ref-62), and it justifies the frozen-rule, no-prior-affiliation, dual-database measurement strategy of Chapter 4.
These five propositions close the chapter and open the next. The literature establishes, at high confidence, that openness is associated with more downstream use; at high confidence, that the article-level evidence cannot identify a causal effect because of selection; and, at high confidence, that the mechanism operates at the level of a data producer, as the Landsat episode shows. It leaves open, because no study in the corpus addresses it, the mission-level identified estimate that the propositions above call for. The remainder of the dissertation assembles the data (Chapter 4), specifies the matched, staggered difference-in-differences design and its identification guards (Chapter 5), and lays out the pre-registered analysis plan and the fixed decision rule (Chapter 6) that will determine whether H1, the proposition that free-and-open release produces a measurable upward break in a mission's downstream publication and dataset-citation yield, is supported or falsified. Consistent with the design-stage guardrail, no such estimate is reported in this chapter or anywhere in the document; the literature is read to specify the design, not to anticipate its result.


# Chapter 4: Data and Measurement

## 4.0 Overview: measurement as the foundation of inference

The measurement scheme of this dissertation converts an institutional argument into a falsifiable estimate, and it is built to defeat one overriding threat: that a change in *counting* will be mistaken for a change in *output*. The chapter's central claim is that the four named data sources, assembled into a mission-period panel with a counting rule frozen across the pre- and post-adoption periods, jointly support a credible measurement of the latent quantity the design targets, the downstream scientific productivity of a NASA Earth-science mission, while remaining honest about every place where the proxy and the truth diverge. The chapter states each source in depth, gives every variable an operational definition keyed to a real instrument or database, names the biases that contaminate each measurement, and specifies the validation and the access-and-ethics regime under which the panel will be built. It does not report results; consistent with the design-stage guardrail, every numerical illustration is labeled as such, and none has been computed on the full assembled panel.

Measurement carries this much weight for a structural reason. The two methodological anchors of the dissertation, Douglass North on institutions and Simon Kuznets on aggregates, both make their bite at the level of measurement rather than estimation. North's claim that an open-data policy lowers the transaction cost of impersonal exchange is testable only if "impersonal use" can be measured as something distinct from "use by the mission team," and credible only if "open" is coded by what the policy actually did to access cost rather than by the label the policy wore [\[85\]](#ref-85). Kuznets's discipline, that an aggregate is a constructed proxy whose error structure must be stated before it is interpreted [\[62\]](#ref-62), is a measurement instruction first and an inference instruction second. A citation count is not scientific productivity; it is a constructed indicator standing in for it, with a known and biased error structure [\[41\]](#ref-41). This chapter is the discharge of that instruction. Build the measurement carelessly, and the cleanest event-study estimator in Chapter 5 will estimate the wrong thing precisely.

The measurement problem this chapter solves is specific. The open-data-advantage literature measures its outcome at the level of the individual article or dataset, where the unit is self-selected into openness and where the count is taken from whatever single database is convenient, leaving the estimate exposed both to author selection and to single-source indexing artifacts [\[63\]](#ref-63), [\[96\]](#ref-96)]. The design requires instead a mission-level outcome, measured from two independent bibliographic sources cross-checked against each other, with the treatment coded from a hand-built register that distinguishes nominal from functional openness, and with an upstream usage measure (distribution logs) that can catch a relabeling masquerading as new use. No assembled dataset of that shape exists for NASA Earth-science missions, and without it any mission-level estimate would inherit the measurement weaknesses of the article-level literature without that literature's one advantage, its large sample. This chapter closes the measurement side of that gap by specifying, in full, the data and the operationalization the design requires.

The chapter proceeds in seven movements. Section 4.1 treats the bibliometric outcome sources, the NASA Astrophysics Data System and Web of Science, and explains the dual-source design as a construct-validity defense. Section 4.2 treats the data-access logs from NASA Earthdata and the Distributed Active Archive Centers as an upstream usage measure and mechanism check. Section 4.3 treats the hand-coded open-data-policy adoption register, its sources, its double-entry protocol, and its handling of phased transitions. Section 4.4 presents the full measurement table mapping every construct to an operational definition, a source, and a scale. Section 4.5 discharges the Kuznets proxy-error statement explicitly. Section 4.6 specifies data quality, validation against known values, and the access-and-ethics regime. Section 4.7 carries the five prospectus limitations forward, each tied to the Chapter 5 or Chapter 6 mitigation that answers it.


## 4.1 Mission-linked publication and citation counts

### 4.1.1 Why two bibliographic sources, not one

The first and most consequential measurement decision is to construct the publication and citation outcomes from two independent bibliographic databases rather than one. A single-source count is not trustworthy as a mission-level outcome, and the dual-source design is the remedy. Every bibliographic database has an idiosyncratic and time-varying coverage frontier: it indexes some venues and not others, expands its coverage over time, and applies its own reference-parsing and citation-linking rules. Larsen and von Ins document that the Science Citation Index covered a *decreasing* fraction of the traditional scientific literature over the period they study, with the shortfall concentrated in fast-growing fields such as computer science and engineering, and they conclude that using a single large database as the dominant source for science indicators is problematic because of this declining and uneven coverage [\[93\]](#ref-93). The connection to the dual-source decision is a construct-validity argument: if a measured rise in a mission's publication count could be produced either by a real rise in research or by a database expanding its coverage of the venues where that research appears, then a single source cannot separate the two, and an apparent treatment effect could be a coverage artifact. The broader bibliometric-methods literature reinforces this, treating database choice as a first-order analytic decision rather than a convenience; Ellegaard and Wallin show that even the bibliometric literature analyzing itself partitions sharply by database and category, with measured impact depending on the source frame [\[86\]](#ref-86).

One caution is preserved deliberately. Two sources do not eliminate coverage bias; they convert an unobservable single-source error into an observable cross-source disagreement. The defense is not that ADS and Web of Science are jointly complete, but that a result appearing in one and not the other is flagged as a candidate artifact and down-weighted, while a result appearing in both is more credibly a real change. The design must still answer the objection that the two sources are not fully independent, because both draw on overlapping publisher feeds and both have expanded coverage over the observation window; a coverage shock common to both would not be caught by cross-checking. This residual is acknowledged, and it is the reason the distribution-log mechanism check in Section 4.2 exists: an outcome that is upstream of publication and is recorded by an entirely different system provides a third, non-bibliometric vantage that no common bibliographic coverage shock can reach.

### 4.1.2 The NASA Astrophysics Data System

The NASA Astrophysics Data System (ADS) is a digital library and indexing service that covers the astronomy, astrophysics, and Earth- and planetary-science literature and supports reference resolution and forward and backward citation linking. Its provenance and architecture are described by Kurtz and colleagues in the foundational overview, which sets out the system's coverage of the refereed and unrefereed literature, its citation- and reference-linking machinery, and its role as a citation index for the disciplines it serves [\[60\]](#ref-60). For this study ADS serves two functions. First, it supplies a publication count: the number of mission-linked refereed articles per mission-period. Second, it supplies a citation count: the number of citations accruing to those articles, and, where the linkage permits, to the datasets themselves.

The provenance matters for the bias statement. ADS is strongest in exactly the disciplines this dissertation studies, the geophysical and Earth-observation literature that cites NASA missions, and it has historically maintained reference and citation linking with attention to the grey literature and to non-journal venues that general-purpose indices undercount [\[60\]](#ref-60). That is an asset for coverage of the relevant field but a liability for cross-source comparability, because ADS's inclusion of venues that Web of Science excludes is one of the systematic differences the dual-source check is designed to surface rather than to erase. The unit of analysis ADS contributes is the article and its citation links; these are aggregated to the mission-period by the bibliographic linkage rule defined in Section 4.4. ADS introduces two known biases: coverage growth over the observation window (the index has expanded what it covers, so a raw count can rise for reasons unrelated to mission output) and linkage incompleteness (an article that uses a mission's data but does not name it in an ADS-parseable way is not linked). Both are handled by freezing the linkage rule across periods and by the cross-source check; neither is eliminated.

### 4.1.3 Web of Science

Web of Science supplies the second, independent bibliographic frame. It provides a citation index with its own venue-selection process, its own reference-parsing, and its own field-normalization tooling. The reason for including it is not redundancy but triangulation: its coverage frontier differs from ADS's, so the intersection of the two is a more conservative and more defensible count than either alone, and the symmetric difference between them is a diagnostic. The construct-validity logic is the one stated in 4.1.1 and grounded in Larsen and von Ins [\[93\]](#ref-93): because each index covers a different and shifting slice of the literature, agreement across the two is evidence that a measured change is real, and disagreement is evidence that it may be a coverage artifact.

A note on the broader set of curated databases is warranted for transparency about what this study does and does not use. Scopus is a third large curated abstract-and-citation database, and Baas and colleagues document its content-selection and quality-assurance processes and its wide global coverage [\[47\]](#ref-47). The design does not adopt Scopus as a primary outcome source, because the two-source ADS-plus-Web-of-Science frame already delivers the independence the construct-validity defense requires, and adding a third bibliometric source would multiply the linkage-rule maintenance burden without adding a vantage that is independent of the common publisher-feed substrate. Scopus is retained as an optional sensitivity source: if a reviewer challenges the headline count, a Scopus-based reccount is available as an additional robustness check, with the same frozen linkage rule applied. This is a measurement-design choice, stated here so that the source frame is fixed before estimation rather than chosen after seeing a result.

### 4.1.4 The two bibliometric outcomes constructed from these sources

Two of the three study outcomes are built from ADS and Web of Science. The first is the publication rate, the count per mission-period of peer-reviewed articles that use the mission's data, identified by the combined linkage rule (mission and instrument name matching, dataset-identifier matching, and acknowledgment-text matching) with the matching rule held fixed across pre- and post-adoption periods. The frozen-rule requirement is not a stylistic preference; it is the operational form of the Kuznets within-versus-relabeling distinction [\[76\]](#ref-76), because a rule that tightened or loosened over time would let a change in counting practice appear as a change in output. A supplementary specification restricts the publication count to articles by authors with no prior affiliation to the mission team, which operationalizes North's "impersonal use," the use by researchers who were not part of the producing institution and who therefore had to pay the access transaction cost the policy is alleged to lower [\[85\]](#ref-85).

The second bibliometric outcome is the dataset-citation rate, the count per mission-period of formal citations to the mission's datasets as first-class scholarly objects. The conceptual basis for treating a dataset as a citable object is the Joint Declaration of Data Citation Principles [\[27\]](#ref-27) and the implementation work that followed it, including the publisher and repository roadmaps of Cousijn and colleagues [\[40\]](#ref-40), Fenner and colleagues [\[33\]](#ref-33), and Starr and colleagues [\[50\]](#ref-50). The measurement reality, however, is that formal data citation became common only recently. Park, You, and Wolfram show, in the field with the most public datasets, that *informal* data citation in the body text of articles is far more common than *formal* data citation in the reference list, with the consequence that data producers do not receive documented, indexable credit at a rate comparable to article authorship [\[42\]](#ref-42). The implication for this study is direct, and it is carried as a fixed design constraint: the dataset-citation outcome is sparse and biased downward in the early part of the observation window, it is therefore analyzed separately rather than pooled with the publication count, and it is restricted to the later window where formal data citation is dense enough to support inference. The dataset-citation arm is reported with explicit power caveats throughout, and the design does not let a null on this low-powered arm be read as a null on the better-powered publication arm.


## 4.2 Data-access logs: Earthdata and the Distributed Active Archive Centers

### 4.2.1 What the logs are and why they belong in the design

The third data source is the distribution and access record of NASA's Earth Observing System Data and Information System (EOSDIS), realized through the Earthdata access infrastructure and the network of Distributed Active Archive Centers (DAACs). The provenance is well documented in NASA's own data-stewardship grey literature. EOSDIS is the agency's large-scale system for archiving and distributing Earth-science data; the system is organized into a set of discipline-specific DAACs established at institutions selected for domain expertise, and the DAACs archive and distribute the vast majority of the data from NASA's Earth-science missions [\[143\]](#ref-143), [\[145\]](#ref-145), [\[147\]](#ref-147)]. The contemporary documentation records the scale of the operation, with holdings measured in petabytes and downloads measured in the billions of files per year [\[143\]](#ref-143), [\[147\]](#ref-147)], and situates EOSDIS as the first large-scale system to facilitate public access to global Earth-system data under a free-and-open policy that NASA's Earth Science Division has maintained since the early 1990s [\[143\]](#ref-143), [\[144\]](#ref-144)].

These logs belong in the design because distribution volume is a usage measure that sits *upstream* of publication on the causal path, and an upstream measure recorded by a non-bibliographic system is exactly what is needed to distinguish new use from improved counting. The reason is mechanical: a researcher must obtain the data before publishing with them, so a download precedes the publication it enables, and the lag between them is the analysis-and-review interval. This is the North mechanism made observable: if free-and-open release lowers the transaction cost of obtaining the data, the first thing it should move is the volume of obtaining, that is, distribution, and only later the volume of publishing [\[85\]](#ref-85). The documented Landsat episode bears this out, in that the 2008 free-and-open switch was followed by a rise in scene distribution from the order of tens of thousands to the order of tens of millions of scenes per year, an order-of-magnitude movement in distribution that preceded and underwrote the subsequent expansion of publications and operational products [\[77\]](#ref-77), [\[122\]](#ref-122)].
### 4.2.2 The two roles the logs play

The distribution logs play two roles, and the design keeps them distinct. As an outcome, distribution volume is the earliest-responding of the three outcomes; it should break sooner and more sharply than publications, because it does not wait for the analysis-and-publication lag. As a mechanism check, the *order* of the breaks is the test: a distribution rise that precedes the publication rise is consistent with the North access-cost mechanism, whereas a publication rise *without* any preceding distribution rise is, under the Kuznets discipline, a signature of relabeling rather than new use, and a fixed falsifier of the contribution [\[76\]](#ref-76). This is the single most important reason the logs are in the design. The bibliometric outcomes can be fooled by a coverage or attribution change common to ADS and Web of Science; the distribution logs cannot be fooled by the same shock, because they are generated by a download-counting system that has nothing to do with how articles are indexed.

### 4.2.3 Known biases and the limits of the log measure

The log measure carries its own biases, and they are stated rather than assumed away. First, distribution counts are sensitive to the unit of distribution and to how the DAAC defines a download event; a change in product granularity (for example, a shift from delivering scenes to delivering analysis-ready tiles) can change the count without changing the underlying use. The design therefore uses distribution as a descriptive early-response and mechanism signal rather than as a precisely calibrated quantity, and normalizes within mission and product line where the documentation permits. Second, automated and machine-to-machine access, including bulk and programmatic retrieval, can inflate raw download counts relative to human-driven analytic use, and the rise of cloud-based and programmatic access over the observation window means this inflation is itself time-varying [\[29\]](#ref-29). Third, the peer-reviewed methodological literature on using DAAC distribution logs as a bibliometric mechanism check is thin; the supporting material is largely NASA's own data-systems grey literature [\[143\]](#ref-143), [\[144\]](#ref-144), [\[145\]](#ref-145), [\[147\]](#ref-147)]. The consequence, flagged in the prospectus and carried here, is that the distribution-volume arm is treated as a corroborating descriptive signal whose direction and timing matter more than its level, and that the headline causal estimate rests on the bibliometric outcomes, with the logs serving as the independent check that the bibliometric movement is real.


## 4.3 The hand-coded open-data-policy adoption register

### 4.3.1 The register as the treatment variable

The treatment in this study is not observed in any single database; it must be constructed. The open-data-policy adoption register is a hand-coded table that records, for each NASA Earth-science mission in scope, the date on which its data transitioned to free-and-open release, the access regime that preceded that transition, and the licensing and tooling status before and after. The register *is* the treatment variable. The entire identification strategy of Chapter 5 rests on the adoption date being coded correctly, so the register receives the most stringent quality protocol of any element in the data architecture.

The register can be coded reliably enough to support a staggered-adoption design, despite the absence of a clean machine-readable source of adoption dates. The source record, though distributed, is rich and contemporaneous: NASA's data-policy documentation establishes the free-and-open posture and its history [\[143\]](#ref-143), [\[144\]](#ref-144), [\[147\]](#ref-147)]; mission-specific documentation and DAAC policy records establish per-mission regimes and transitions [\[74\]](#ref-74); and the policy-history literature provides the regulatory and programmatic context that disambiguates experimental from operational data regimes for U.S. Earth-observation systems [\[138\]](#ref-138). Triangulating these contemporaneous sources, with double entry and adjudication, yields an adoption code more reliable than any single document, in the same way the dual bibliographic sources yield a more reliable count. Some transitions are genuinely phased rather than instantaneous. The objection a careful reader will raise, that a phased transition has no single "adoption date," is answered not by forcing a false precision but by flagging phased cases and testing sensitivity to alternative date definitions, as 4.3.3 specifies.

### 4.3.2 The coding protocol: double entry and adjudication

The coding protocol is designed to make the register's error structure visible and bounded. Each mission is coded independently by two coders working from the same source dossier, and the two codings are compared. Agreements are accepted; disagreements are adjudicated against the source documents by a third reviewer, and the basis for the adjudicated decision is recorded. Inter-coder agreement is computed and reported as a data-quality statistic, so that the reliability of the treatment variable is a stated quantity rather than an assumption. This protocol mirrors the construct-validity logic used for the FAIR-based openness coding: openness is coded by what the policy did to access cost, not by the word "open" in a document, using the FAIR vocabulary to separate nominal accessibility from functional findability, interoperability, and reusability [\[9\]](#ref-9), [\[80\]](#ref-80), [\[120\]](#ref-120)]. A mission whose data are nominally open in license but functionally encumbered (for example, open in principle but inaccessible in practice for want of tooling or discoverable identifiers) is flagged, and the robustness analysis in Chapter 5 reclassifies such cases to test whether the headline estimate depends on counting functionally encumbered missions as treated.

### 4.3.3 Phased transitions, the prior regime, and what the register records

For each mission the register records four fields beyond identity: the adoption date (or date range, for phased cases), the prior access regime (restricted, fee-based, registration-gated, or embargoed), the licensing status before and after, and the tooling-and-identifier status before and after. The prior-regime field is what makes the comparison group meaningful: a mission that moved from a fee-based regime to free-and-open has experienced a larger drop in access transaction cost than one that moved from a registration-gated but free regime, and the design can use the prior-regime field to test whether the effect scales with the size of the access-cost reduction. That is the sharpest available test of the North mechanism. Phased transitions are flagged explicitly and handled in two ways: the primary specification uses a coded best-estimate adoption date, and a sensitivity specification re-estimates under alternative date definitions (earliest plausible, latest plausible, midpoint) to confirm that the event-study path is not an artifact of where within a phased window the date was placed. Ambiguous cases that cannot be coded with acceptable confidence are excluded and the exclusion is documented, so that coverage is a transparent and reconstructable set rather than a silent judgment call.


## 4.4 Operationalization: the measurement table

This section maps every construct in the design to an operational definition, a data source, and a measurement scale. The table is the operational core of the chapter; Appendix A reproduces it as the formal data dictionary. The variable definitions are carried verbatim from the shared design bible and are not redefined here; what this section adds is the source-and-scale specification for each.

**Table 4.1. Construct-to-measurement mapping.**

| Construct | Operational definition | Source | Scale |
|---|---|---|---|
| Publication rate (Outcome 1) | Count, per mission-period, of peer-reviewed articles using the mission's data, identified by the frozen combined linkage rule (mission and instrument name + dataset-identifier + acknowledgment-text matching) | ADS [\[60\]](#ref-60); Web of Science; cross-checked | Non-negative integer count per mission-year (quarter in robustness); structural zeros expected for small or young missions |
| Impersonal publication rate (Outcome 1, supplement) | Outcome 1 restricted to articles whose authors have no prior mission-team affiliation | ADS + Web of Science + author-affiliation resolution | Non-negative integer count per mission-period |
| Dataset-citation rate (Outcome 2) | Count, per mission-period, of formal citations to the mission's datasets as first-class objects under the JDDCP definition | ADS dataset-citation linking; Web of Science Data Citation linkage | Non-negative integer count per mission-period; restricted to later window; low power flagged [\[42\]](#ref-42) |
| Distribution volume (Outcome 3) | Access and download events per mission-period from the archive distribution record | Earthdata / DAAC distribution logs [\[143\]](#ref-143), [\[145\]](#ref-145), [\[147\]](#ref-147)] | Non-negative count (files or scenes) per mission-period; descriptive early-response and mechanism signal |
| Treatment (open-data adoption) | Indicator turning on in the mission's coded transition period to free-and-open release | Hand-coded adoption register [\[74\]](#ref-74), [\[138\]](#ref-138), [\[144\]](#ref-144)] | Binary, staggered-onset; absorbing (no coded reversions in scope) |
| Prior access regime | Categorical prior regime preceding adoption | Adoption register | Categorical: restricted / fee-based / registration-gated / embargoed |
| Functional-openness flag | Whether nominal openness is matched by FAIR functional accessibility | Register coding under FAIR vocabulary [\[9\]](#ref-9), [\[80\]](#ref-80), [\[120\]](#ref-120)] | Binary flag; drives reclassification robustness check |
| Sensor class (matching covariate) | Instrument class of the mission's primary sensor | Mission documentation | Categorical: optical imager / SAR / lidar / passive microwave / spectrometer |
| Mission age (matching covariate) | Periods elapsed since the mission's operational start at each period | Mission documentation | Non-negative integer (periods) |
| Research-community size (considered control) | Size of the relevant research community for the mission's domain | Bibliometric field-size estimate | Continuous / ordinal proxy |
| Data-product maturity (considered control) | Maturity level of the mission's standard data products | Mission / DAAC product documentation | Ordinal level |
| Agency / international partner (considered control) | Sole-NASA versus joint or international-partner mission | Mission documentation | Categorical |

Two operationalization decisions in the table deserve explicit defense. First, the unit of every outcome is the mission-period count, and the period is the year in the primary specification and the quarter in a robustness specification. The year is chosen as primary because the bibliometric outcomes accrue with a lag measured in years, and because annual aggregation reduces the structural-zero problem that plagues quarterly counts for small missions; the quarterly robustness specification exists to confirm that annual aggregation does not smooth away the timing information that the distribution-log mechanism check relies on. Second, the structural zeros are treated as real, not missing: a young mission that has generated no mission-linked publications in a period has a true count of zero, and the count-appropriate modeling specified in the bible (Poisson or log-link with attention to structural zeros) is the reason the outcome is left as a raw count rather than logged with an ad hoc offset. This is a measurement decision with estimation consequences, and it is fixed here so that it cannot be chosen after seeing the data.


## 4.5 The Kuznets proxy-error statement

The Kuznets discipline requires that the error structure of the outcome proxy be stated in full before any inference is drawn, and this section discharges that requirement [\[62\]](#ref-62). The publication and citation counts are constructed proxies for the latent quantity of scientific productivity, not the quantity itself, and their biases are known, named, and partially correctable. The stance is the one Henderson, Storeygard, and Weil adopt for night-lights as a proxy for economic activity: the proxy is combined with, and disciplined by, an awareness of its noise rather than asserted to be the truth [\[41\]](#ref-41).

Five error properties are stated. First, **right-skew**: citation and publication counts are heavily right-skewed and over-dispersed, with a small number of missions and articles accounting for a large share of the mass; the modeling and inference choices in Chapter 5 (count models, wild-cluster bootstrap) respond to this property, and the proxy is never treated as approximately normal. Second, **accrual lag**: citations accumulate over years after publication, so a recent mission-period's citation count is mechanically lower than an older period's for reasons unrelated to quality, and the event-study specification, which compares each post-adoption period to the normalized pre-adoption baseline within cohort, is partly chosen to net out the common accrual profile. Third, **field-size and citation-norm dependence**: a mission serving a large, high-citing community will show higher counts than an equally productive mission serving a small community, which is why sensor class and the considered community-size control enter the matching, and why effect heterogeneity by sensor class is estimated rather than averaged away. Fourth, **indexing-coverage sensitivity**: as established in 4.1 and grounded in Larsen and von Ins, the count depends on which venues the source database indexes and on how that coverage changed over time [\[93\]](#ref-93); the dual-source design and the frozen linkage rule are the defenses, and the cross-source disagreement is the diagnostic. Fifth, **attribution-practice drift**: the rise of formal data-citation norms over the window means that the *same* underlying use can be counted differently in late periods than in early ones [\[27\]](#ref-27), [\[40\]](#ref-40), [\[42\]](#ref-42)], which is precisely the relabeling channel the design must block, and which the frozen linkage rule and the no-prior-affiliation specification are built to block.

The decisive move, drawn directly from McMillan and Rodrik, is the refusal to read a rise in the aggregate as a rise in real output until the relabeling channel has been excluded [\[76\]](#ref-76). McMillan and Rodrik decompose productivity growth into a genuine within-component and a reallocation component and show that apparent transformation can be mere relabeling that does not raise true aggregate output; the analog here is that an apparent rise in mission-linked publications could be a real increase in new research or a change in how existing research is attributed and indexed once data citation became easier and was encouraged. The measurement architecture answers this in three layers: the linkage rule is frozen across periods so a counting change cannot masquerade as an output change; the no-prior-affiliation specification isolates impersonal new use; and the distribution logs provide an upstream, non-bibliographic check, since a publication rise unaccompanied by a distribution rise is read as relabeling and falsifies [\[76\]](#ref-76). Confidence in the proxy is therefore stated as *moderate and conditional*: moderate because the biases are real and only partially correctable, conditional because the proxy earns a productivity interpretation only when the frozen-rule count, the impersonal-use count, and the distribution signal move together. Evidence that would *raise* confidence is convergence across all three; evidence that would *lower* it is a publication movement without a distribution movement, or a movement that appears in one bibliographic source but not the other.


## 4.6 Data quality, validation against known values, and access and ethics

### 4.6.1 Data quality controls
Each source carries a quality protocol matched to its failure mode. For the bibliometric sources, the controls are the frozen linkage rule, the dual-source cross-check, and a reported linkage-precision and linkage-recall audit on a hand-validated sample of mission-article pairs, so that the bibliographic measurement error becomes a stated quantity rather than an assumption. For the adoption register, the control is the double-entry-and-adjudication protocol of 4.3.2 with reported inter-coder agreement and a documented exclusion log for uncodable missions. For the distribution logs, the control is normalization within mission and product line, together with the explicit treatment of distribution as a directional and timing signal rather than a calibrated level, given the granularity and machine-access biases of 4.2.3.

### 4.6.2 Validation against a known value

The strongest available validation is against a known benchmark, and the benchmark is the Landsat distribution series. The assembled distribution-volume measure can be checked for fidelity by reproducing a documented, externally established fact: the order-of-magnitude rise in Landsat scene distribution following the 2008 free-and-open policy switch. Wulder and colleagues and the fifty-year Landsat retrospective document this rise from the order of tens of thousands to the order of tens of millions of scenes annually, and tie it explicitly to the policy change [\[77\]](#ref-77), [\[122\]](#ref-122)]. The validation test is direct: when the study's distribution-volume series is constructed for Landsat, it should reproduce this documented break in level and timing. If it does, the distribution-measurement pipeline is validated against a known value, and the mechanism-check role of the logs is credible for the other missions; if it does not, the pipeline is mis-specified and must be corrected before any mission's distribution series is trusted. The independent bibliometric validation of the same episode is available too. Hemati and colleagues, surveying fifty years of Landsat change-detection studies, document that the average number of Landsat images used per study rose from roughly ten before 2008 to the order of one hundred thousand by 2020, a publication-side corroboration of the same policy break drawn from Web of Science and Scopus rather than from distribution logs [\[82\]](#ref-82). Reproducing both the distribution-side and the publication-side Landsat break is the central validation-against-known-values exercise of the data build, and it is specified here as a pass/fail gate before the full panel is estimated.

A second, internal validation is the cross-source agreement statistic between ADS and Web of Science on the publication and citation counts. High agreement on missions and periods where no coverage change is suspected supports the joint reliability of the two sources; systematic divergence localized to a particular venue class or period flags a coverage shock to investigate before estimation. This is validation in the construct-validity sense rather than against an external truth, but it is the appropriate check for the bibliometric arm, where no external gold-standard count exists.

### 4.6.3 Access and ethics

The access-and-ethics posture is straightforward, and it is itself an instance of the principle under test. All four sources are either openly accessible or accessible under standard institutional terms. The bibliometric counts derive from ADS, which is openly available, and from Web of Science, accessed under institutional subscription; the distribution logs derive from NASA's EOSDIS, whose data have been distributed under a free-and-open policy since the early 1990s [\[143\]](#ref-143), [\[144\]](#ref-144), [\[147\]](#ref-147)]; the adoption register is compiled from public mission and policy documentation [\[74\]](#ref-74), [\[138\]](#ref-138)]. No human-subjects data, no personally identifying information beyond published author names and affiliations, and no restricted or sensitive data are involved; the only personal data are the author-affiliation records used to construct the impersonal-use specification, drawn from the public bibliographic record and used only to classify authorship relative to mission teams, not to profile individuals. The reproducibility commitment is explicit and forms the ethical center of the design: the analysis code, the hand-coded adoption register with its sources, and the linkage rules are intended for release so that the panel can be reconstructed and the event-study path reproduced. This is not incidental. The dissertation studies whether making data open and reusable raises their downstream scientific use; the evidence for or against that claim should itself be as open and reusable as the mission data whose openness is under test, and the FAIR principles that govern the openness coding are applied to the study's own outputs as well as to the missions it studies [\[120\]](#ref-120).


## 4.7 Coverage and the five carried limitations

The chapter closes by carrying the five limitations stated in the prospectus forward, each tied to the specific mitigation that answers it, so that the strength of any eventual claim is bounded by the weakest of these rather than the strongest. Coverage is the set of NASA Earth-science missions for which a clear access regime and adoption date can be coded and for which bibliographic linkage is feasible; the limitations are properties of that set and of the measurements taken over it.

First, **indexing coverage is incomplete and time-varying** in both ADS and Web of Science [\[93\]](#ref-93). The mechanism by which this threatens the design is that a coverage expansion can raise a count without raising output; the mitigation is the dual-source cross-check and the frozen linkage rule, which together convert an invisible single-source error into a visible cross-source diagnostic and prevent a counting change from masquerading as an output change. This limitation is answered in the construct-validity defenses of Chapter 5.

Second, **the adoption date is sometimes phased rather than a clean event**. The mechanism is that a phased transition has no single onset, so a mis-placed date contaminates the event-time alignment; the mitigation is the phased-transition flag and the alternative-date sensitivity analysis of 4.3.3, with the sensitivity result reported so that the path's robustness to date definition is shown rather than assumed.

Third, **formal data citation is sparse in the early window** [\[27\]](#ref-27), [\[42\]](#ref-42)]. The mechanism is that the dataset-citation outcome is mechanically near-zero early and rises as norms develop, which would confound a norm change with a treatment effect; the mitigation is to restrict the dataset-citation arm to the later window, analyze it separately from the publication arm, and report it with explicit power caveats so that a low-powered null is never read as a substantive null.

Fourth, **the number of codable missions is modest**, on the order of tens rather than hundreds, with thin matching pools for some sensor classes. The mechanism is that small samples make conventional asymptotic inference unreliable and make some matched comparisons fragile; the mitigation is the wild-cluster bootstrap and the heterogeneity-robust estimators specified in Chapter 5, the minimum-detectable-effect analysis that states the design's power honestly, and the reporting of effect heterogeneity by sensor class rather than a single pooled effect that thin pools cannot support.

Fifth, **bibliographic linkage of a publication to a mission is itself imperfect**, because authors name missions, instruments, and datasets inconsistently, so the linkage rule introduces measurement error that, if it changed over time, would be confounded with the treatment. The mechanism is the relabeling channel of 4.5; the primary mitigation is freezing the linkage rule across periods, the secondary is the no-prior-affiliation specification that isolates impersonal use, and the tertiary is the distribution-log mechanism check that no bibliographic linkage error can reach. This is the limitation most tightly bound to the dissertation's central measurement claim, and it is the reason the chapter's architecture is built, as stated at its opening, to defeat the mistaking of a change in counting for a change in output.

Taken together, these five limitations and their mitigations complete the obligation that this chapter owes the larger argument. Measurement is where the stakes concentrate: a mission-level outcome must be measured, the article-level literature's measurement weaknesses must not be inherited, and the entire causal estimate is only as good as the proxy and the treatment code. The chapter answers that demand at the level of the mechanism, since the distribution logs make North's access-cost channel observable and the frozen rule makes Kuznets's relabeling channel blockable, and it earns its place over a cheaper single-source, single-instant, unfrozen measurement that would be wrong. What it cannot fully remove is named, bounded, and routed to a specific downstream mitigation, limitation by limitation. The measurement is therefore specified to a standard at which the design-stage estimate, once executed, can be interpreted as evidence about productivity rather than as an artifact of counting, the precondition the two anchors jointly impose and the one this chapter exists to satisfy.


# Chapter 5: Research Design and Identification

## 5.0 Overview: the estimator and the problem it solves

The empirical design of this dissertation is a matched, staggered-adoption difference-in-differences event study, estimated with the Callaway and Sant'Anna group-time average-treatment-effect apparatus [\[14\]](#ref-14), that compares the downstream scientific output of NASA Earth-science missions before and after their transition to free-and-open data release against the contemporaneous output of matched restricted-access missions. The rest of this chapter defends that design. It states why this estimator and not a simpler one, writes the specification out in the notation fixed by the shared bible, argues the identification assumptions formally, enumerates every threat to validity with its mitigation, specifies a robustness battery and a power analysis in advance, and commits the whole design to pre-registration before any estimation touches the assembled panel.

The problem this chapter must solve is one of credibility, not of computation. The open-data-advantage evidence base repeatedly associates openness with more downstream citation, but almost always at the level of the individual article or dataset, where the comparison is contaminated by author self-selection: better-resourced research is both more likely to be made open and more likely to be cited, so the cross-sectional association cannot be read as the effect of openness [\[34\]](#ref-34), [\[63\]](#ref-63)]. What is needed is a mission-level estimate in which the treatment is a policy event rather than an author choice, and in which the counterfactual is a defensible comparison group rather than an assumption that open and closed research are otherwise identical. That is an identification gap, and it is the gap this chapter is built to close, because until it is closed NASA and the Jet Propulsion Laboratory keep weighing the cost of open-release infrastructure (Distributed Active Archive Center operation, product curation, access tooling) against a benefit asserted from episodes and anecdote rather than estimated under a stated counterfactual.

The chapter proceeds through eight movements: the estimator and the case against the naive alternative (5.1); the specification written out (5.2); the identification assumptions argued formally (5.3); the matching layer and its costs and benefits (5.4); the four-part validity audit with mitigations (5.5); the pre-specified robustness battery (5.6); the power and minimum-detectable-effect analysis (5.7); and the pre-registration commitment and computational plan (5.8). Throughout, the design is held to the two methodological anchors fixed in the bible. North supplies the causal mechanism the design must isolate, the lowering of the transaction cost of access, and the prediction of a path-dependent, gradual response that motivates a dynamic rather than a single-coefficient design [\[85\]](#ref-85). Kuznets supplies the measurement discipline that keeps the outcome from being read naively, the insistence that a citation count is a constructed proxy with a stated error structure and that a rise in the proxy must be shown to be new output rather than improved counting before it is read as productivity [\[41\]](#ref-41), [\[62\]](#ref-62), [\[76\]](#ref-76)]. Every numerical value in this chapter that describes a result, a coefficient, a power figure, or a detectable effect is labeled illustrative or expected and has not been computed on the full assembled panel; the design is complete, the estimation is not.

## 5.1 The estimator, and why the naive alternative is rejected

The correct estimator for this design is the Callaway and Sant'Anna group-time average treatment effect on the treated, and the two-way fixed-effects (TWFE) event-study regression that an applied reader would reach for first is not merely less efficient but actively biased in this setting and must be rejected as the primary estimator.

The case begins with the structure of the data. Adoption of free-and-open release is staggered: NASA Earth missions transitioned at different calendar dates, some early, some late, and some not at all within the observation window [\[143\]](#ref-143), [\[147\]](#ref-147)]. The treatment effect is, by the North mechanism, expected to be heterogeneous across missions (a large optical-imager user community responds differently from a thin passive-microwave one) and dynamic in event time (the response builds over post-adoption periods as user communities and workflows form). Staggered timing combined with heterogeneous, dynamic effects is precisely the configuration under which the justification for the naive estimator fails.

The reason these features force the rejection of TWFE is the Goodman-Bacon decomposition [\[35\]](#ref-35). Goodman-Bacon shows that the TWFE coefficient in a staggered design is a weighted average of all possible two-group, two-period difference-in-differences comparisons embedded in the panel, and that this average includes "forbidden" comparisons in which already-treated units serve as controls for later-treated units. When treatment effects are dynamic, the trajectory of an already-treated unit is still changing, so using it as a control subtracts off part of the very effect being estimated, and the implied weights can be negative. The result is that the TWFE coefficient can carry the wrong sign even when every unit-level effect is positive. This is not a small-sample worry; it is a bias in the estimand itself. The supporting evidence is broad and convergent: de Chaisemartin and D'Haultfoeuille reach the same negative-weighting conclusion from an independent decomposition [\[30\]](#ref-30); Sun and Abraham show the contamination specifically for the event-study coefficients that this design relies on, demonstrating that a given lead or lag coefficient absorbs effects from other event times under heterogeneity [\[113\]](#ref-113); Baker, Larcker, and Wang document empirically that correcting for this bias frequently moves published staggered-DiD effects toward zero, so the problem is consequential in practice and not only in theory [\[1\]](#ref-1); and the Roth, Sant'Anna, Bilinski, and Poe synthesis catalogues the failure modes and the menu of robust alternatives [\[53\]](#ref-53).

A caveat is owed here, and protecting it is part of doing this honestly. The bias of TWFE is not universal. Rüttenauer and Aksoy show by Monte Carlo that a TWFE specification including a flexible event-time function can perform well, and that all estimators, robust and naive alike, remain equally vulnerable to violations of parallel trends, anticipation, and time-varying confounding [\[114\]](#ref-114), [\[115\]](#ref-115)]. Wooldridge sharpens the point further by proving an equivalence between an extended TWFE estimator and a pooled-OLS Mundlak regression that controls for cohort indicators, period indicators, covariates, and their interactions, recovering the heterogeneity-robust ATT through flexible regression [\[46\]](#ref-46). The honest reading is therefore not that TWFE is always wrong but that the simple TWFE is unreliable under exactly the conditions this design faces, and that the robust estimators do not rescue the design from the assumptions all of them share. This caveat does not overturn the case for the chosen estimator; it bounds it. The primary estimator is chosen because it makes the aggregation weights explicit and non-negative by construction, not because it relaxes parallel trends, which no estimator in this family does.
This yields the estimator choice with high confidence as to the direction of the argument and moderate confidence as to magnitude, given that the relevant simulations are calibrated to settings that differ from a tens-of-missions Earth-science panel. The Callaway and Sant'Anna estimator computes, for each adoption cohort and each period, a clean two-period comparison against a control group drawn only from not-yet-treated and never-treated units, never from already-treated ones, and then aggregates the cohort-time effects with transparent weights [\[14\]](#ref-14). It makes the forbidden comparison impossible rather than merely diagnosable.

The internal logic of the estimator is worth stating mechanically, because the design's defensibility rests on it. The building block is a single cohort-by-period comparison. For cohort g and period t, the estimator forms the change in outcome for the treated cohort from its baseline period g-1 to t, and subtracts the change over the identical calendar interval for a comparison group composed only of units that were not yet treated, or never treated, as of t. Because the comparison group is restricted in this way, the trajectory being differenced out is a genuine untreated trajectory, not a trajectory that is itself still moving under an earlier treatment. The estimator offers two distinct constructions of that comparison group, and the design must choose between them deliberately rather than by default. The not-yet-treated comparison uses, at each period t, all missions whose own adoption lies strictly after t, which maximizes the comparison sample and exploits the staggered timing most aggressively but rests on the assumption that the timing of later adoption is unrelated to the outcome path. The never-treated comparison uses only missions that never adopt within the window, which is cleaner in that those units carry no treatment contamination at all but smaller and, in this Earth-science setting, drawn from a pool of restricted-access missions whose comparability is the hardest to defend. The design's default is the not-yet-treated comparison, with the never-treated comparison reported as a robustness arm, because the staggered structure of NASA adoption supplies a rich not-yet-treated pool that a never-treated-only design would waste, and because Athey and Imbens show that under as-good-as-random adoption timing the staggered comparison recovers an interpretable weighted average causal effect [\[101\]](#ref-101). The choice is recorded in the pre-registration of Section 5.8 so that it cannot be switched after seeing which comparison gives the larger effect.

## 5.2 The specification, written out

This section writes the specification in the notation fixed by the bible and carried verbatim, so that the design does not drift from its siblings. The mechanism reasoning is stated alongside the algebra: the specification is the form the North prediction takes once it is made estimable.

For adoption cohort g, defined as the set of missions that adopted free-and-open release in period g, and for period t, the primary estimand is the group-time average treatment effect on the treated,

\[
\operatorname{ATT}(g,\,t) = \mathbb{E}\!\left[\, Y_t(g) - Y_t(0) \mid G = g \,\right] \qquad\qquad (1)
\]

where \(Y_t(g)\) is the potential outcome of a mission under adoption in period \(g\), \(Y_t(0)\) is the never-treated potential outcome, and \(G\) is the adoption cohort. \(\operatorname{ATT}(g,t)\) is the average, over missions that adopted in \(g\), of the difference between the outcome they realized and the outcome they would have realized had they never adopted. It is identified by comparing the change in outcome for cohort \(g\) from the last pre-adoption period \(g-1\) to period \(t\) against the same-calendar change for a comparison group of not-yet-treated and never-treated missions, taken within matched sensor-class-by-age strata. The matched-strata qualification is load-bearing and is defended in Sections 5.3 and 5.4; without it the comparison group is the full mission pool, and an optical imager is being differenced against a synthetic-aperture-radar mission of unlike user community and unlike secular trend.

The cohort-time effects are aggregated into a dynamic event-study path indexed by event time \(e = t - g\),

\[
\theta(e) = \sum_{g} w_{g} \cdot \operatorname{ATT}(g,\, g+e) \qquad\qquad (2)
\]

with cohort weights \(w_g\) proportional to cohort size, and into an overall summary effect that averages \(\theta(e)\) over the post-adoption event window. The last pre-adoption period, \(e = -1\), is normalized to zero, so every coefficient is read relative to the period immediately before treatment. The leads, the coefficients at \(e < 0\), test for differential pre-trends: under valid identification they should be jointly indistinguishable from zero. The lags, the coefficients at \(e \geq 0\), trace the dynamic effect: under H1 with the North mechanism, they should be small at \(e = 0\) and grow over subsequent event times as the path-dependent adjustment unfolds, because a user community that grew up under restricted access does not reconfigure its workflows the instant the rule changes.

The outcome is a non-negative count (mission-linked publications per mission-period; formal dataset citations per mission-period; distribution events per mission-period), so the conditional mean is modeled in a count-appropriate form. The default is a Poisson or log-link specification, estimated within the Callaway and Sant'Anna framework, with explicit attention to the structural zeros that are common for small or young missions whose downstream output in a given period is genuinely zero rather than missing. A log-of-counts transformation is rejected as the default because log(0) is undefined and the ad hoc log(y+1) fix distorts the small-count behavior that dominates this panel; the count-link specification handles the zeros natively. The choice of scale carries an interpretive commitment that the design states openly: on a count or log-link scale, the parallel-trends assumption is an assumption about proportional, not additive, untreated trajectories, and a difference-in-differences that is justified on one scale need not be justified on the other. Barkowski's analysis of nonlinear difference-in-differences makes this precise, showing that the parallel-trends assumption and the interpretation of the estimated effect both shift with the link function, so the design fixes the scale of its parallel-trends claim in advance and conducts its leads test and sensitivity analysis on that same scale, rather than asserting parallel trends on levels and then estimating on a log link [\[104\]](#ref-104). Standard errors are clustered at the mission level, because the mission is the unit at which treatment is assigned and within which periods are serially correlated. Given a modest number of mission clusters, the asymptotic cluster-robust variance is supplemented by the wild-cluster bootstrap, whose role in the inference plan is detailed in Sections 5.5 and 5.7.

The estimable model behind the count link can be stated compactly. Let \(Y_{it}\) be the count outcome for mission \(i\) in period \(t\), let \(D_{it}\) be the binary treatment indicator equal to one once mission \(i\) has adopted, and let the conditional mean be modeled multiplicatively so that \(\mathbb{E}[Y_{it} \mid \cdot]\) is the exponential of a mission effect, a period effect, the matching-stratum controls, and a sum of event-time terms each of which carries the coefficient \(\theta(e)\) for the corresponding lead or lag. The Callaway and Sant'Anna procedure does not estimate this as a single saturated regression, which is what reintroduces the contamination Sun and Abraham identify [\[113\]](#ref-113); instead it estimates the cohort-time \(\operatorname{ATT}(g,t)\) as separate clean comparisons and then aggregates them into the \(\theta(e)\) of the event-study path. The regression form above is therefore the interpretive scaffold, the object that connects the estimand to a familiar event-study picture, while the actual estimation runs through the cohort-time building blocks. Stating both is deliberate: the regression form makes the specification legible to a reader who reasons in regressions, and the building-block form is what the estimation actually executes and what keeps the aggregation weights non-negative.

This specification is the estimable form of the conceptual model: access cost falls, distribution rises first, impersonal publication rises with a lag, and formal dataset citation rises later still. The event-study path lets the design observe the lag structure that the mechanism predicts, rather than collapsing it into a single before-after number that the mechanism says would be misspecified.

## 5.3 Identification: the assumptions argued formally

The design identifies \(\operatorname{ATT}(g,t)\), and therefore \(\theta(e)\), under a conditional parallel-trends assumption defined within matched strata, together with a no-anticipation assumption and an overlap condition, and each of these is stated as a falsifiable commitment rather than asserted.

The central assumption is conditional parallel trends. Formally: for each cohort g and each post-adoption period t, the expected change in the never-treated potential outcome \(Y_t(0)\) from \(g-1\) to \(t\) is equal for the treated cohort and for its matched comparison group, conditional on the matching covariates (sensor class and mission age). In words, absent the open-data policy, the publication and citation trajectories of treated missions would have evolved in parallel to those of their matched comparison missions. What makes this plausible rather than heroic is the matching layer and the staggered timing: an optical imager that went open is compared with optical imagers of similar age that did not, so the comparison holds fixed the two characteristics most likely to drive differential secular trends in scientific output, namely the size and growth of the user community (proxied by sensor class) and the maturation of the data products (proxied by mission age). The propensity-score and matching literature establishes when conditioning on observed covariates makes a parallel-trends-type assumption defensible [\[99\]](#ref-99), [\[111\]](#ref-111)], and the specific result that matching prior to difference-in-differences can reduce bias when parallel trends would otherwise fail, at a cost in variance that must be acknowledged [\[24\]](#ref-24), [\[81\]](#ref-81)].

The second assumption is no anticipation: missions do not change their downstream output in advance of adoption in response to the impending policy. This is plausible here because the downstream actors are external researchers who use the data, not the mission team, and external researchers cannot publish using data they cannot yet access. The no-anticipation assumption is also testable through the leads: anticipation would show up as non-zero coefficients in the periods immediately before \(e = -1\), and the design checks for exactly this. The third assumption is overlap, or common support: for every matched stratum there must exist both treated and comparison missions over the relevant event window, or the \(\operatorname{ATT}\) for that stratum is not identified. Overlap is not assumed but verified, and strata that fail it are reported as outside the support rather than extrapolated into.

One limit must be protected: parallel trends is fundamentally untestable for the post-adoption periods, because the counterfactual \(Y_t(0)\) for treated missions after adoption is never observed. The leads test the assumption only over the pre-adoption window, and a flat-leads finding is evidence consistent with parallel trends, not proof of it. Roth shows that conditioning the analysis on having passed a pre-trends test introduces its own distortion, because the test has limited power and the act of selecting on it biases the subsequent estimates [\[100\]](#ref-100). The design responds not by trusting the pre-trends test alone but by carrying the Rambachan and Roth sensitivity framework, which replaces the binary "trends are parallel" assumption with a reported region: how large a post-adoption violation of parallel trends, expressed as a multiple of the observed pre-trend variation, would be required to overturn the estimated effect [\[97\]](#ref-97). The identified effect is therefore reported as a robustness region rather than a point, and the confidence attached to any causal reading is conditional and, at the design stage, moderate at best. The staggered timing keeps this from collapsing: not-yet-treated missions supply comparison information at every adoption period, so the design does not lean entirely on never-treated missions, whose comparability is the hardest to defend [\[14\]](#ref-14), [\[101\]](#ref-101)].

The several pre-adoption periods this panel offers are not merely a passive test of the assumption; they are an active source of identifying strength, and the design exploits them as such. Egami and Yamauchi show that multiple pre-treatment periods serve three distinct purposes that a single pre-period design cannot: they assess parallel trends with more than one degree of freedom, they improve estimation accuracy, and they permit a weaker, more flexible parallel-trends assumption that allows for a common pre-existing trend rather than requiring strict level parallelism [\[83\]](#ref-83). The design adopts the flexible reading wherever the pre-period record supports it, because requiring strict parallelism when a common linear trend would suffice discards information and risks rejecting a valid comparison on a technicality. This is also where the choice between the not-yet-treated and never-treated comparison groups re-enters the identification argument rather than only the estimand: the not-yet-treated comparison identifies the ATT under a parallel-trends assumption that need only hold between the treated cohort and units adopting later, a strictly weaker requirement than parallelism against a never-treated pool that may differ systematically because it never adopted at all. The design thus reads identification as a graded, not binary, property: strongest where balanced strata, flat leads, a flexible-trend specification, and a wide Rambachan-Roth breakdown threshold all coincide, and explicitly downgraded, with the causal language softened to association, wherever any of those four supports is weak.

## 5.4 Matching and balance: the comparison group constructed before the difference

Matching restricted-access comparison missions to open-access treated missions on sensor class and mission age, before estimating the difference-in-differences, is the right way to construct the counterfactual, and that decision carries a stated cost that the design accepts deliberately rather than ignores.

The raw mission pool is heterogeneous in exactly the dimensions that drive scientific output independently of data policy. Sensor class is a proxy for the size and disciplinary breadth of the latent user community, and mission age is a proxy for data-product maturity; both shift the publication trajectory whether or not the mission ever goes open. Differencing a young optical imager against an old passive-microwave mission would confound the policy effect with these structural differences. Matching rests on the Rosenbaum and Rubin result that conditioning on the propensity score, the probability of treatment given covariates, balances the covariate distributions between treated and comparison groups and so removes the confounding that those covariates would otherwise introduce [\[99\]](#ref-99). The procedure follows Stuart's guidance on matching method, distance metric, and the sequence of estimating the propensity model, forming matched sets, and checking balance before any outcome model is fit [\[111\]](#ref-111). Because the propensity model can itself be misspecified, the covariate-balancing propensity score of Imai and Ratkovic is carried as the default estimator, since it estimates the treatment-assignment model while directly optimizing covariate balance and so withstands the mild misspecification that plagues plain logistic propensity models [\[59\]](#ref-59).

Balance is not assumed from the act of matching; it is measured and reported. The diagnostic is the standardized difference in covariate means between matched groups, with the Austin convention that an absolute standardized difference below roughly one-tenth indicates adequate balance, reported alongside variance ratios and the distribution of the propensity score across groups [\[8\]](#ref-8). Austin's emphasis is precisely that significance tests of balance are the wrong diagnostic, because they conflate sample size with imbalance; the standardized difference is preferred because it measures the magnitude of imbalance on a scale that does not shrink merely because the matched sample is small, which matters acutely here where the matched sample will be small by construction [\[8\]](#ref-8). The estimation proceeds only if balance is acceptable; if it is not, the matching specification is revised (caliper, ratio, covariate set) before, never after, the outcome is examined, so that the matching choice cannot be tuned to the result. The matching ratio is itself a design parameter with a power consequence: one-to-many matching retains more comparison information and raises power but admits less similar controls and so risks residual imbalance, while one-to-one matching maximizes similarity at the cost of discarding comparison missions the thin pool can ill afford. The design fixes the ratio in advance against the balance threshold rather than choosing it to maximize the apparent effect, and Xiao's hands-on propensity-score workflow is followed for the operational sequence of defining the question, selecting covariates, estimating the score, matching, checking balance, and only then estimating the effect, with the matched structure respected in the variance calculation rather than ignored [\[49\]](#ref-49).

A subtle inference question arises once matching precedes the difference-in-differences: whether the uncertainty from the matching step should itself be propagated into the standard errors of the treatment effect. The design treats the matched comparison as fixed for the primary estimate, consistent with the convention that the matched design defines the sample on which the DiD is then estimated, but it also reports a bootstrap that resamples through the matching step, because Zhu and Su show that whether to bootstrap through propensity-score matching materially affects the estimated variance in an economic-modeling causal-inference setting and that ignoring the matching step can understate uncertainty [\[117\]](#ref-117). Reporting both the matching-fixed and the matching-bootstrapped intervals is the honest accounting; the wider of the two is treated as the operative interval for the falsification rule, so that a borderline-significant effect is not declared significant on the strength of an understated variance.

The cost is stated plainly and is the protected qualifier of this section. Matching before difference-in-differences is not free: it reduces the effective sample by discarding unmatched units and it raises the variance of the estimate even as it lowers bias. Ham and Miratrix formalize this benefit-cost tension, showing that matching helps when parallel trends would otherwise be violated but can hurt mean squared error when it would have held [\[24\]](#ref-24); Ge and Ham extend the analysis to the variance and mean-squared-error side that the bias-only literature had left unexplored, and find that matching on observed covariates prior to DiD is not unconditionally preferable to the unmatched estimator once the sample-size tradeoff is counted, though matching additionally on pre-treatment outcomes is always beneficial because it removes that tradeoff [\[81\]](#ref-81). The design responds by reporting both the matched and the unmatched estimates and by treating the matched estimate as primary only where balance diagnostics justify it, which is an honest accounting of the cost rather than a claim that matching is costless. Confidence in the matched design is moderate and explicitly conditional on the balance diagnostics clearing the Austin thresholds.
## 5.5 Threats to validity, each with its mitigation

This section audits the design against the four classical validity types and pairs each threat with the design feature that mitigates it. The structure follows the Campbell tradition (internal, external, construct, statistical-conclusion), and every mitigation named here is a commitment carried into the pre-registration of Section 5.8.

### 5.5.1 Internal validity

The central internal threat is a violation of parallel trends through selection on trends: missions may adopt open release precisely when their scientific output is already rising, for example as the mission matures and its data products stabilize, so that the post-adoption rise reflects a pre-existing trajectory rather than the policy. The mechanism by which this would bias the estimate is direct. If treated missions were already on a steeper output path, the difference-in-differences attributes that steeper path to the treatment. Three defenses are deployed against it. First, the event-study leads test directly for pre-adoption divergence; under H1 with valid identification the leads are flat, and positive trending leads are a specific falsifier that halts any causal reading regardless of the lag pattern. Second, the Roth diagnostics assess whether the leads test has the power to detect the trend violations that would matter, guarding against a false sense of security from an underpowered flat-leads finding [\[100\]](#ref-100). Third, the Rambachan and Roth sensitivity analysis reports the breakdown threshold, the magnitude of post-adoption differential trend, scaled to the observed pre-trends, that would be needed to overturn the effect, converting the binary assumption into a reported region [\[97\]](#ref-97). Maturation, the rival in which output rises because missions age rather than because they go open, is handled by making mission age both a matching covariate and an explicit control, so that the comparison is between missions of like age and the age trajectory is differenced out [\[14\]](#ref-14).

A second internal threat is a concurrent policy shock: a directorate-wide change, the arrival of a new data system, or a cross-cutting funding shift that coincides in calendar time with a mission's adoption and that moves output for reasons unrelated to that mission's own policy [\[145\]](#ref-145), [\[147\]](#ref-147)]. Here a calendar-time shock common to a whole cohort would be misattributed to the cohort's adoption. The design has two defenses. The matched comparison group is drawn from missions of the same era, so a shock common to the era is differenced out as long as it hits treated and comparison missions alike; this is the central reason the comparison group is era-contemporaneous rather than pooled across the whole window. And the cohort-specific \(\operatorname{ATT}(g,t)\) estimates reveal whether the apparent effect clusters on a single calendar date across cohorts in a way that would signal a common shock rather than an adoption effect, because a true adoption effect should track event time, which is staggered, whereas a calendar shock should track calendar time, which is shared. The Callaway and Sant'Anna decomposition into cohort-time cells is what makes this diagnostic available; a pooled estimator would hide it [\[14\]](#ref-14).

### 5.5.2 External validity

The estimate applies to NASA Earth-science missions in the observation window and may not transfer to other agencies, to non-Earth missions, or to future missions in a changed publishing environment. The Landsat record suggests the access-cost mechanism is strong in optical remote sensing, where a large latent user community was held back chiefly by cost and price, and where the 2008 free-and-open switch was followed by an order-of-magnitude rise in distribution and a marked expansion in publications and operational products [\[77\]](#ref-77), [\[122\]](#ref-122), [\[132\]](#ref-132)]. The mechanism need not be equally strong for sensor classes with smaller communities or where the binding constraint is analysis capacity rather than access. The mitigation is to estimate and report effect heterogeneity by sensor class rather than averaging it away, treating the sensor-class profile as the honest boundary of generalization. The Copernicus user-uptake evidence is carried as an external reference point that the access-cost mechanism generalizes beyond a single program, while also showing that uptake depends on tooling and community support, not on license terms alone [\[68\]](#ref-68). Confidence in external transfer is low and is stated as such; the design does not claim a uniform effect across mission types when its own estimates are built to show variation.

The sensor-class heterogeneity is not a nuisance to be tolerated but a direct test of the North mechanism, and stating it that way sharpens what the heterogeneity estimates are for. The mechanism says that open release raises downstream use by lowering the transaction cost of access, which can only matter where a latent user community exists that the access cost was holding back. Where that latent community is large (optical imagers feeding land-cover, agriculture, fire, and change-detection literatures), the access cost is the binding constraint and the predicted effect is large; the Landsat record is the canonical instance, with distribution rising from tens of thousands to tens of millions of scenes after 2008 and the publication base expanding correspondingly [\[77\]](#ref-77), [\[122\]](#ref-122)]. Where the latent community is small, or where the binding constraint is analysis capacity or instrument-specific expertise rather than access, the same policy lowers a cost that was not the one holding use back, and the predicted effect is small. The design's sensor-class cuts therefore operationalize a mechanism prediction: the effect should be ordered by the size of the latent user community, largest for the broad optical imagers and smaller and noisier for the specialized classes. A finding that contradicted that ordering, a large effect concentrated in a thin-community class, would not merely bound external validity; it would be evidence against the access-cost mechanism itself and would push the interpretation toward a counting or attribution change under the Kuznets discipline. The heterogeneity estimates are thus doing double duty, marking the boundary of generalization and adjudicating between the North mechanism and its relabeling rival, which is why they are pre-registered as a confirmatory rather than an exploratory output.

The design commits to reporting its domain of validity as a two-column ledger, following the units-treatments-outcomes-settings framework that Shadish, Cook, and Campbell use to bound quasi-experimental transport [\[101\]](#ref-101). The left column states what the design can speak to: units are NASA Earth-science missions with a codable open-data-policy adoption date, sensor classes with at least three matched comparison missions in the observation window, and data-product maturity sufficient for bibliographic linkage under the frozen rule; the treatment is a transition to free-and-open release, combining license change and persistent-identifier assignment, within the observation window; outcomes are mission-linked peer-reviewed publication rates and, in the later window, formal dataset-citation rates, both constructed under the frozen bibliographic rule; and the setting is the NASA data-distribution infrastructure as it stood in the observation window, with DAAC and Earthdata as the access layer. The right column states what it cannot speak to without further evidence: missions at other agencies or under other national programs; sensor classes too thin or too specialized to form a matched comparison pool; open-data transitions that changed only the license without changing tooling, discoverability, or DAAC-supported access; outcomes defined by informal citation practices or by download events alone; and future settings in which the publishing environment, citation norms, or the baseline access regime differ materially from the observation window. This ledger is a pre-registration commitment, not a post hoc qualification: the population boundary is stated before the panel is assembled so that any mission the data force out of the analysis can be evaluated against the registered inclusion scope rather than absorbed silently into the estimation, and the results section will carry it unchanged alongside the headline estimates.

### 5.5.3 Construct validity

Two constructs are at risk: the outcome and the treatment. The outcome, a citation or publication count, is a proxy for the latent quantity of scientific productivity, and the Kuznets discipline requires that a rise in the proxy be shown to be new output rather than improved counting [\[62\]](#ref-62), [\[76\]](#ref-76)]. The specific failure mode is the McMillan-Rodrik relabeling analog: after a mission goes open, more authors may name the mission or cite its dataset because citation became easier and was encouraged by data-citation norms, inflating the count without any new research [\[27\]](#ref-27), [\[33\]](#ref-33)]. The mitigations are three and are built into the variable construction of Chapter 4 and carried here: the matching rule that links a publication to a mission is held fixed across pre- and post-adoption periods, so a change in counting practice cannot masquerade as a change in output; a supplementary specification restricts to authors with no prior mission-team affiliation, isolating impersonal use in North's sense; and the distribution-volume outcome from Earthdata and DAAC logs serves as an independent mechanism check, because a publication rise unaccompanied by any distribution rise is read, under the Kuznets discipline, as relabeling and is itself a falsifier. The treatment is also a construct: nominal openness is distinguished from functional openness using the FAIR vocabulary, so that a mission coded open in license but functionally encumbered, open but practically inaccessible for want of tooling, is reclassified in a robustness check rather than counted as treated [\[120\]](#ref-120). A second construct threat is single-database indexing: a count drawn from one bibliographic source may move because the source's coverage changed, not because output changed. The dual-source design (ADS cross-checked against Web of Science) is the defense, since a change visible in one index but not the other is more likely an artifact than a real effect [\[60\]](#ref-60).

### 5.5.4 Statistical-conclusion validity

The counts are right-skewed and over-dispersed, the number of missions is modest (tens, not hundreds), and clustering is at the mission level, so conventional asymptotic inference may be unreliable and the risk is a false-positive effect from understated standard errors. Over-dispersion is addressed by the count-link specification with attention to the variance-mean relationship rather than an imposed Poisson equidispersion. The small-cluster problem is addressed by the wild-cluster bootstrap, which delivers valid inference with a modest number of clusters where the cluster-robust asymptotic variance does not, and by the heterogeneity-robust estimators that avoid the negative-weighting variance pathologies. The dataset-citation arm is reported with explicit power caveats because formal data citation is sparse in the early window; the design does not overstate an outcome it knows to be thinly measured. Multiplicity, the risk of a spurious significant lead or lag among many estimated coefficients, is handled by reporting the joint test of the leads and the aggregated overall effect as the primary inferential objects rather than cherry-picking an individual event-time coefficient. Confidence in the statistical-conclusion layer is moderate, conditional on the bootstrap and the over-dispersion handling behaving well at the realized cluster count, which Section 5.7 examines directly.

## 5.6 The robustness battery, specified in advance

The headline result must not depend on a single estimator or a single set of design choices, and the full set of robustness checks is fixed here, before estimation, so that agreement across them is informative rather than a product of post hoc selection. Pre-specifying the battery is what makes a convergent result credible; choosing the checks after seeing the primary estimate would turn the battery into a search.

The first layer is estimator triangulation. The event-study path is re-estimated with four alternative heterogeneity-robust estimators whose biases and efficiency properties differ, so that convergence across them is evidence the result is not an artifact of one estimator's internals. The Sun and Abraham interaction-weighted estimator addresses the event-study contamination from a saturated-regression angle [\[113\]](#ref-113). The Borusyak, Jaravel, and Spiess imputation estimator fits the untreated model on the controls and imputes treated counterfactuals, which is the efficient estimator under unrestricted heterogeneity and a useful contrast to the Callaway and Sant'Anna two-period building blocks [\[10\]](#ref-10), [\[58\]](#ref-58)]. The de Chaisemartin and D'Haultfoeuille estimator provides a further robust path, including its imperfect-parallel-trends extension that bears directly on a design that cannot guarantee exact parallel trends [\[17\]](#ref-17), [\[30\]](#ref-30)]. The Wooldridge extended-TWFE / Mundlak equivalence is included as a regression-based cross-check that recovers the heterogeneity-robust ATT through pooled OLS, a transparency benefit because its mechanics are legible to readers unfamiliar with the newer estimators [\[46\]](#ref-46).

The second layer is design-variant triangulation. Synthetic difference-in-differences is carried as a check suited to a sparse, staggered panel with few treated units, because it reweights both units and periods to build a comparison series and holds up where a tens-of-missions panel strains the standard estimator; the Esposti application to sparse, staggered EU rural-development adoption is the closest design precedent for using it under exactly this small-and-staggered condition [\[98\]](#ref-98), [\[129\]](#ref-129), [\[130\]](#ref-130)]. Stacked difference-in-differences is carried as a second design variant that builds a clean dataset of treated-and-control event windows around each adoption, with the corrective sample weights that Wing, Freedman, and Hollingsworth show are required for the stacked estimator to identify a sensible aggregate rather than a weight-distorted one [\[18\]](#ref-18). A generalized two-by-two building-block estimator of the Kennedy-Shaffer form is noted as a further non-parametric cross-check that targets the same aggregate from weighted two-period comparisons [\[65\]](#ref-65).

The third layer is specification and coding robustness. The adoption date is re-coded under alternative definitions for missions whose transition was phased rather than a clean event, and the effect is re-estimated under each; sensitivity to the date definition is reported rather than hidden. The functional-openness reclassification described in 5.5.3 is run as a robustness arm. The matched and unmatched estimates are both reported per Section 5.4. The period granularity is varied from years to quarters in a robustness specification. And the nonlinear-DiD interpretation caution of Barkowski is carried, because the parallel-trends assumption has a different meaning on a count or log scale than on a level scale, and the design states which scale its parallel-trends claim is made on so that the robustness checks are comparing like with like [\[104\]](#ref-104). The result is reported as robust only where it survives this battery; a result that appears under the primary estimator but evaporates under the variants is reported as fragile, not as a finding.

A fourth layer guards the pre-trends test itself, because the robustness of a flat-leads claim is as important as the robustness of the lags. The imputation-based estimators that the second layer uses for the lags also produce placebo pre-trend estimates, and Li and Strezhnev show that the common practice of imputing control outcomes with the same in-sample model used for the treated counterfactuals introduces two biases into those placebo estimates, an attenuation bias from redundant differences that are zero by construction and a contamination bias from using early adopters as controls, with the result that the pre-trends can look flatter than they are [\[133\]](#ref-133), [\[134\]](#ref-134)]. The lesson, carried into the analysis plan, is that the leads must be estimated with a leave-one-out construction done separately by adoption-timing group, not with the default in-sample imputation, so that a reassuring flat-leads picture is not an artifact of the placebo construction. This guards directly against the specific failure in which a design declares identification valid on the strength of pre-trends that its own estimator flattened. The convergence the battery seeks is therefore convergence on both ends of the event-study path, flat leads under a properly constructed placebo and positive lags under multiple robust estimators, not convergence on the lags alone.

A fifth commitment pre-registers a bright-line minimum-comparison-unit rule for thin cohort-time cells. The Callaway and Sant'Anna estimator aggregates \(\operatorname{ATT}(g,t)\) estimates across cells, and a cell in which the clean not-yet-treated comparison pool falls to a single mission is not analytically unworkable, but its weight in the aggregated headline could be disproportionate and its contribution fragile. The pre-registered rule is: any \((g,t)\) cell in which the matched comparison pool contains fewer than three missions is excluded from the primary aggregation; its individual \(\operatorname{ATT}(g,t)\) is still estimated and reported in the cohort-time table so that no information is silently discarded, but it does not contribute to the headline event-study path or the summary effect used to evaluate the decision rule of Section 6.2. Cells excluded by this rule are listed in the deviation report described in Section 5.8, and the headline effect is re-estimated including them as a sensitivity check, so the reader can see what the bright-line costs in power relative to what it gains in aggregation stability. This commitment closes the gap that arises when a one-comparison-mission cell enters the aggregate: such a cell cannot diagnose a differential pre-trend within its stratum, cannot support the wild-cluster bootstrap reliably, and can place a weight on the aggregate that a single unusual mission could drive. Setting the threshold at three rather than two is pre-registered rather than chosen after inspecting the realized cell counts; three is the minimum at which a within-cell trend test has any degrees of freedom and at which the bootstrap can operate without degeneracy. This threshold may be revised downward to two by the deviation protocol only if the assembled panel shows that no sensor-class stratum has three not-yet-treated comparison missions in any post-adoption period, in which case the revision is reported as a deviation with its justification alongside the registered analysis [\[14\]](#ref-14).

## 5.7 Power and the minimum detectable effect

The design has a candidly limited but non-trivial ability to detect the effect it is looking for; this ability is quantified in advance through a minimum-detectable-effect (MDE) analysis rather than discovered after a null result, and the dataset-citation arm is the weakest and is flagged as such before estimation.

The reasons for taking power seriously are structural. The number of distinct Earth-science missions with codable access regimes is on the order of tens, the matching pool for some sensor classes is thin, and the outcomes are over-dispersed counts. Each of these reduces effective power: few clusters widen the bootstrap intervals, thin strata limit the within-class comparisons, and over-dispersion inflates the variance of a count outcome above the Poisson benchmark. An explicit MDE analysis rather than a vague acknowledgment is needed because a null result in an underpowered design is uninformative: it cannot distinguish "no effect" from "an effect too small for this panel to see," and the falsification rule fixed in advance (failure to reject H0 falsifies the contribution) only has teeth if the design could have detected an effect of policy-relevant size had one existed. Naoki Egami and Yamauchi's double-DiD result, that multiple pre-treatment periods improve estimation accuracy and permit a more flexible parallel-trends assumption, supports exploiting the several pre-adoption periods this panel offers to recover power that a single pre-period design would forfeit [\[83\]](#ref-83).

The procedure, design-stage and not yet executed, is a simulation-based power analysis. The data-generating process is calibrated to the assembled panel's realized features: the number of missions, the cohort sizes, the event-time window, the empirical over-dispersion of the count outcomes, and the mission-level serial correlation. For a grid of true effect sizes, expressed as a proportional increase in the mission-linked publication rate relative to the matched comparison path, the simulation draws repeated synthetic panels, applies the full estimation and inference pipeline including the wild-cluster bootstrap, and records the rejection rate. The MDE is read off as the smallest true effect for which the design rejects H0 with the conventional probability at the chosen size. As an illustrative target, and labeled illustrative because it has not been estimated, the analysis is oriented toward detecting a proportional increase in the publication rate on the order of one quarter to one half by several event-time periods after adoption, which is the rough magnitude the Landsat record makes plausible for a strong-community sensor class [\[77\]](#ref-77), [\[122\]](#ref-122)]; whether the assembled panel achieves power against an effect of that size is exactly what the simulation will report, and the honest expectation is that power will be adequate for the publication arm in the larger sensor classes and marginal for the thin ones.

The MDE analysis also confronts a structural feature of small-cohort staggered designs that a single aggregate power figure would conceal: power is not uniform across event time, because the composition of cohorts contributing to each event-time coefficient changes as the window widens. Coady, Wing, and colleagues' trimmed-aggregate construction makes the point that comparisons over event time can confound a dynamic effect with a compositional change unless the contributing set is held balanced [\[18\]](#ref-18), and the implication for power is that the longer post-adoption lags, which draw on fewer cohorts that have been observed that far past adoption, are the least well powered. The simulation therefore reports the MDE by event time, not only in aggregate, so that a flat coefficient at a long lag is correctly read as low power rather than as a fading effect. Chib and Shimizu's Bayesian cohort-time-stratum framework is noted as a complementary route that stabilizes inference in sparse cohort-by-time-by-stratum cells by partial pooling, which is exactly the sparsity this panel exhibits, and is carried as a sensitivity check on the thinnest strata where the frequentist cell estimates are least stable [\[102\]](#ref-102).
The dataset-citation arm carries the protected qualifier. Formal data citation became common only recently, so this outcome is available for the later part of the window and over fewer periods, which compounds the small-cohort problem with a short panel. The design commits in advance to reporting the dataset-citation MDE separately and to refusing to read a null on that arm as evidence of no effect, because the power to detect one is expected to be low; the arm is reported as exploratory and is not allowed to carry the headline. The distribution-volume arm, by contrast, is expected to be the best-powered, because download events are numerous and respond immediately, and it is positioned as the early-response and mechanism check precisely because its power is highest and its lag is shortest. The expected ordering of power across the three outcomes (distribution highest, publication intermediate, dataset citation lowest) is itself a testable feature of the design rather than an excuse: if the mechanism holds, the best-powered outcome should also be the earliest to break, and a design that found a publication break with no detectable distribution break would face the relabeling falsifier of Section 5.5.3 regardless of how the power fell out.

## 5.8 Pre-registration commitment and the computational plan

The entire design above is committed to pre-registration before estimation, and the analysis is implemented in a documented, reproducible computational pipeline, so that the evidence for or against H1 is itself as open and reusable as the mission data whose openness is under test.

The pre-registration commitment is specific. Fixed before any estimation touches the assembled panel are: the outcome definitions and the frozen linkage rule; the matching covariates, distance metric, ratio, and balance thresholds; the choice of the not-yet-treated comparison as primary with never-treated as a robustness arm; the primary estimator and the four-plus robustness estimators named in Section 5.6; the event-time window and the normalization of \(e = -1\) to zero; the count-link scale on which the parallel-trends claim is made; the leave-one-out placebo construction for the leads; the clustering level and the wild-cluster bootstrap; the matching-bootstrapped variance as the operative interval; the Rambachan and Roth sensitivity breakdown threshold; the sensor-class heterogeneity cuts; and the decision rule and falsification conditions carried verbatim from the bible.

No design survives contact with real data unaltered, so the pre-registration also fixes a deviation protocol. That protocol separates a credible pre-analysis plan from a brittle one. Any departure that the assembled data force, say a sensor-class stratum with no codable comparison missions, or an adoption date that cannot be coded cleanly, is reported as a deviation with its reason, and the registered analysis is reported alongside the deviated one wherever both are feasible, so a reader can see what the change did to the result. Decisions the plan could not anticipate are labeled exploratory and barred from contributing to the confirmatory test of H1. This converts the inevitable mid-study judgment calls from a hidden source of researcher degrees of freedom into a documented, auditable trail, the only honest way to run a pre-registered observational design where the data, unlike in an experiment, were not generated to the plan's specification. That rule, fixed and not to be altered after seeing results, is that support for H1 requires jointly flat leads, positive lags with a positive and statistically distinguishable overall effect, and survival of the Rambachan and Roth sensitivity analysis at the stated threshold; failure on any one of those, or a publication rise without a distribution rise, falsifies the contribution. The case for pre-registration is the specification-search critique: a design with this many defensible analytic forks could, if the forks were chosen after seeing the data, manufacture a significant result from noise, and the only protection is to fix the forks in advance and report deviations as deviations. Pre-specifying the robustness battery is what makes cross-estimator agreement informative rather than selected [\[53\]](#ref-53).

The computational plan names the toolchain so the pipeline is reproducible rather than described in the abstract. The Callaway and Sant'Anna estimator and its aggregation and event-study machinery are implemented through the established `did` toolchain; the staggered-design diagnostics and the alternative estimators through the corresponding `staggered`, imputation, and synthetic-DiD packages; the parallel-trends sensitivity analysis through the `HonestDiD` implementation of the Rambachan and Roth framework [\[97\]](#ref-97); the covariate-balancing propensity score and balance diagnostics through the matching toolchain of the Imai and Ratkovic and Austin references [\[8\]](#ref-8), [\[59\]](#ref-59)]; and the wild-cluster bootstrap through a documented bootstrap routine appropriate to the realized cluster count. The pipeline is organized as a numbered, scripted sequence (panel assembly, outcome and covariate construction under the frozen rule, matching and balance reporting, primary estimation, lead and sensitivity testing, robustness re-estimation, heterogeneity estimation, and the distribution and dataset-citation repeats) so it runs end to end from the raw inputs and can be re-run by a third party. The analysis code, the hand-coded adoption register with its sources, and the linkage rules are intended for release. Reproducibility here is not a procedural nicety but an instance of the very mechanism the dissertation studies: the cost of verifying and reusing this study's evidence should fall toward the cost of a download, exactly as the open-data policy under test lowers the cost of reusing a mission's data.

## 5.9 Chapter synthesis: how the design advances the argument

The design assembled in this chapter advances every part of the dissertation's argument for which it is responsible. It reaches the causal mechanism rather than mere correlation through the matched, staggered event study that isolates the policy event from secular trends and mission characteristics and estimates the access-cost mechanism North predicts, with distribution logs as an independent upstream check [\[14\]](#ref-14), [\[85\]](#ref-85), [\[99\]](#ref-99), [\[111\]](#ref-111)]. Its advantage over the simpler options is secured by the explicit rejection of the naive TWFE estimator under the Goodman-Bacon decomposition, of the article-level association that cannot remove self-selection, and of the single-mission Landsat before-after that has no contemporaneous control [\[30\]](#ref-30), [\[34\]](#ref-34), [\[35\]](#ref-35), [\[63\]](#ref-63), [\[113\]](#ref-113)]. What remains uncertain is held within tolerable bounds by the four-part validity audit, the pre-specified robustness battery, the candid power analysis with its dataset-citation caveat, and the frozen, pre-registered decision rule that makes both a positive and a null result reportable and neither foreclosed [\[10\]](#ref-10), [\[62\]](#ref-62), [\[76\]](#ref-76), [\[97\]](#ref-97), [\[100\]](#ref-100), [\[120\]](#ref-120)].

What this chapter cannot do, and does not claim to do, is deliver an estimate. The estimator is chosen, the specification is written, the identification is argued, the threats are mitigated, the robustness battery is fixed, the power is bounded, and the pipeline is committed to pre-registration, but no \(\operatorname{ATT}(g,t)\), no event-study coefficient, and no robustness region has been computed on the full assembled panel, and every numerical magnitude named here is labeled illustrative or expected for that reason. The confidence the design supports is conditional and, at this stage, moderate at its strongest: high confidence that the estimator and identification strategy are the right ones for the data structure, moderate confidence that the matched comparison will clear its balance diagnostics, and low confidence that the effect, if present, will transfer beyond the sensor classes with large user communities. Chapter 6 turns this design into the step-by-step, pre-registered analysis plan and the specified-but-unpopulated result templates on which H1 will finally be supported or falsified.


# Chapter 6: Analysis Plan and Expected Results

This chapter answers one question before any data are touched: exactly what will be done to the assembled panel, in what fixed order, and by what fixed rule the resulting event-study path will be read as support for H1 or as a failure to reject H0. The answer is a pre-registered pipeline. The pipeline runs from panel assembly through outcome construction with a frozen counting rule, matched comparison-group formation with reported balance, the Callaway and Sant'Anna group-time event study [\[14\]](#ref-14), a lead-based pre-trend test with Roth power diagnostics [\[100\]](#ref-100), a pre-specified robustness battery [\[10\]](#ref-10), [\[30\]](#ref-30), [\[113\]](#ref-113)], the Rambachan and Roth sensitivity analysis [\[97\]](#ref-97), sensor-class heterogeneity estimation, and parallel repeats for the distribution-volume and dataset-citation outcomes. The decision rule that maps this path onto the hypothesis is fixed verbatim from the shared bible and stated before any estimation. Every number in this chapter is labeled expected or illustrative. None has been computed on the full assembled dataset, and the result tables are laid out with their column headers, event-time rows, and sensitivity-region templates in place but their cells deliberately empty. That emptiness is a design choice, not an omission: a populated cell here would be a fabricated finding, and the integrity of a pre-registered plan depends on its arriving at the data with the cells blank.

The problem this chapter addresses is specific to the design stage of an identified causal study. By the close of Chapter 5 the project holds a complete estimator, a complete identification argument, and a complete measurement apparatus, but no fixed decision procedure connecting the estimator's output to the hypothesis. What remains is to specify that procedure so completely that a third party, handed the panel and the code, would arrive at the same accept-or-reject conclusion the candidate would, with no room for the post hoc specification search that the open-data-advantage literature has repeatedly fallen prey to [\[63\]](#ref-63). The analysis plan itself is that missing piece: the ordered pipeline, the fixed rule, and the pre-registered expectations. Absent it, the heterogeneity-robust machinery of Chapter 5 could still be undermined by analyst degrees of freedom exercised after seeing the event-study coefficients, which would return a mission-level study to the same credibility problem that afflicts the article-level evidence base it is meant to improve upon. This chapter answers that need by writing the procedure and the rule down in advance and committing to them.

## 6.1 The estimation procedure as a fixed pipeline

### 6.1.1 Why the order is fixed and not merely listed

The estimation procedure is presented as a numbered pipeline whose order is itself a pre-registered commitment, not a convenience of exposition. Fixing the order of operations is a substantive identification guard, not a stylistic one. Several steps in the pipeline are gates: each one can halt the analysis or change its interpretation, and a gate placed after the step it is meant to discipline cannot do its job. The pre-test literature establishes why order matters. Roth [\[100\]](#ref-100) shows that conditioning an event-study interpretation on a pre-trend test run after the analyst had already seen the dynamic coefficients distorts inference, because the analyst's choices become correlated with the realized estimates. The broader replication-crisis evidence reinforces the point, showing that researcher degrees of freedom, exercised in an unfixed order, inflate false-positive rates across empirical fields, alongside the systematic-review finding that the open-data-advantage magnitude is contested precisely because selection and specification choices vary across studies [\[63\]](#ref-63). Fixing the order constrains the candidate, not the data: it cannot make a poorly identified design well identified, and it does not substitute for the matching and sensitivity steps it sequences. It must withstand the objection that an overly rigid pipeline could prevent legitimate, data-driven diagnosis of an unforeseen data problem; the plan answers this by distinguishing pre-registered inferential steps, which are frozen, from descriptive data-quality checks, which may be run at any time and reported transparently as deviations. Confidence in the value of a fixed order is high, because it rests on a published, directly applicable result [\[100\]](#ref-100) rather than on analogy.

### 6.1.2 Step 1: panel assembly

The first step assembles the mission-period panel by linking the bibliographic, access-log, and treatment-register sources described in Chapter 4 into a single unbalanced panel indexed by mission and period. Publication and citation records from the NASA Astrophysics Data System and from Web of Science are linked to each mission using the frozen bibliographic linkage rule, which combines mission and instrument name matching, dataset-identifier matching, and acknowledgment-text matching, with the rule held fixed across the pre- and post-adoption periods. Earthdata and Distributed Active Archive Center distribution logs are merged at the mission-period level to supply the distribution-volume outcome. The hand-coded adoption-date register attaches, to each mission, the period of transition to free-and-open release, the prior access regime, and the licensing and tooling status before and after. The panel is unbalanced by construction because missions enter and exit the observation window at different times and because some never adopt open release within the window; never-adopters and not-yet-adopters are retained because they supply comparison information for the group-time estimator. The output of this step is a single analysis table whose row is a mission-period and whose columns are the three outcomes, the adoption cohort indicator, and the matching covariates. No estimation occurs in this step; its sole product is the linked panel, and any record that cannot be unambiguously linked is flagged rather than dropped silently, so that linkage attrition is itself a reported quantity.

### 6.1.3 Step 2: outcome and covariate construction under the frozen rule

The second step constructs the three outcomes and the matching covariates using the construction rules fixed in Chapter 4, the central one being that the bibliographic counting rule is frozen across periods. The publication rate is the count, per mission-period, of peer-reviewed articles that use the mission's data under the fixed matching rule, with a supplementary version restricted to articles by authors with no prior affiliation to the mission team, isolating impersonal use in North's sense [\[85\]](#ref-85). The dataset-citation rate is the count, per mission-period, of formal citations to the mission's datasets as first-class objects following the data-citation principles [\[27\]](#ref-27) and the repository roadmap [\[33\]](#ref-33), constructed only for the later part of the window where formal data citation is non-trivial. The distribution volume is the count of access and download events per mission-period from the logs. The matching covariates are sensor class and mission age at each period. This step precedes matching, and the counting rule is frozen before any outcome is examined, for a reason that follows the Kuznets measurement discipline: a citation count is a constructed proxy for the latent quantity of scientific productivity, with a known and biased error structure, and a change in how that proxy is counted must not be allowed to masquerade as a change in the underlying quantity [\[62\]](#ref-62). Freezing the rule across periods is the operational form of that discipline. The mechanism reasoning is direct: if the matching rule were allowed to loosen in the post-adoption period, for example by adding acknowledgment-text patterns that became common only after data-citation norms spread, the post-adoption counts would rise for a counting reason rather than a productivity reason, and the McMillan and Rodrik relabeling problem, in which apparent growth is reattribution rather than new output, would contaminate the estimand [\[76\]](#ref-76). Confidence that the frozen rule addresses relabeling at the construction stage is moderate to high; it removes the most obvious counting drift but cannot remove drift in the indexing coverage of the source databases themselves, which is why the dual-source design and the distribution-log mechanism check remain necessary downstream.

### 6.1.4 Step 3: matching and balance, with a proceed-or-revise gate

The third step matches restricted-access comparison missions to open-access treated missions on sensor class and mission age, using the propensity-score framework of Rosenbaum and Rubin [\[99\]](#ref-99) and the matching guidance of Stuart [\[111\]](#ref-111), and reports covariate balance using the standardized-difference diagnostics of Austin [\[8\]](#ref-8). This step contains the first hard gate in the pipeline: the analysis proceeds to estimation only if post-matching balance is acceptable on the pre-specified standardized-difference threshold; otherwise the matching specification is revised and balance re-checked before any event-study coefficient is computed. Matching before differencing improves the credibility of the conditional parallel-trends assumption rather than merely decorating it. An optical imager that went open is a more plausible counterfactual for another optical imager of similar age than for the full pool of missions of every sensor class and vintage, because the unmodeled determinants of a mission's publication trajectory, the size of its instrument's user community, the maturity of its data products, the breadth of its scientific applications, are themselves correlated with sensor class and age. The propensity-score result that conditioning on the probability of treatment given observed covariates suffices to balance those covariates between groups [\[99\]](#ref-99), combined with Stuart's demonstration that matching reduces the model-dependence of the subsequent estimate [\[111\]](#ref-111), is what licenses the step. The balance-diagnostic literature gives the standardized difference a defensible threshold and warns against relying on the t-test of balance in a matched sample [\[8\]](#ref-8). One limit is essential and is carried explicitly: matching balances only observed covariates, so the gate certifies observable comparability, not unobservable comparability, and the parallel-trends assumption on unobservables is still tested separately by the leads in Step 5. The gate must also survive the case that matching in a sample of tens of missions can exhaust the comparison pool for a thin sensor class, leaving a treated mission with no acceptable match; the plan pre-commits to reporting any such unmatched treated missions and to estimating the effect both with and without them, rather than silently dropping them, because their exclusion would change the population the estimand describes.

### 6.1.5 Step 4: the Callaway and Sant'Anna event study

The fourth step estimates the dynamic event-study path with the Callaway and Sant'Anna group-time estimator [\[14\]](#ref-14), using the notation carried verbatim from the shared bible. For adoption cohort g and period t, the estimand is the group-time average treatment effect on the treated,

\[
\operatorname{ATT}(g,\,t) = \mathbb{E}\!\left[\, Y_t(g) - Y_t(0) \mid G = g \,\right] \qquad\qquad (1)
\]
where \(Y_t(g)\) is the potential outcome under adoption in period \(g\), \(Y_t(0)\) the never-treated potential outcome, and \(G\) the adoption cohort. \(\operatorname{ATT}(g,t)\) is identified by comparing the change in outcome for cohort \(g\) from period \(g-1\) to \(t\) against the same-calendar change for a comparison group of not-yet-treated and never-treated missions, within matched sensor-class-by-age strata. The group-time effects are aggregated into a dynamic event-study path indexed by event time \(e = t - g\),

\[
\theta(e) = \sum_{g} w_{g} \cdot \operatorname{ATT}(g,\, g+e) \qquad\qquad (2)
\]

with cohort weights \(w_g\) proportional to cohort size, and into an overall summary effect. The last pre-adoption period, \(e = -1\), is normalized to zero, so that leads (\(e < 0\)) test pre-trends and lags (\(e \geq 0\)) trace the dynamic effect. Outcomes enter in a count-appropriate form, a Poisson or log-link specification with attention to the structural zeros common for small or young missions, and standard errors are clustered at the mission level with a wild-cluster bootstrap given the modest number of clusters. This estimator is the primary one, rather than the two-way fixed-effects regression an analyst might reach for by default, because of the Goodman-Bacon decomposition. Under staggered timing and treatment effects that grow over event time, the two-way fixed-effects coefficient is a weighted average of all possible two-group, two-period comparisons, including forbidden comparisons that use already-treated missions as controls for later-treated ones. It can place negative weights on some of those comparisons, so that a uniformly positive set of true effects can produce a negative pooled coefficient [\[35\]](#ref-35). The Callaway and Sant'Anna estimator avoids this by never using an already-treated mission as a control and by reporting the effect cohort by cohort and event time by event time before any aggregation [\[14\]](#ref-14). Confidence that the estimator choice is correct for this setting is very high, because the conditions that break two-way fixed effects, staggered adoption and dynamic heterogeneous effects, are the conditions the North mechanism predicts: a path-dependent, gradual response that builds over post-adoption periods [\[85\]](#ref-85).

### 6.1.6 Step 5: the lead-based pre-trend test and its power diagnostics

The fifth step tests the leads of the event study for a differential pre-trend and reads that test through the Roth power diagnostics [\[100\]](#ref-100). The estimated leads \(\theta(e < 0)\) are examined jointly: under valid identification and the H1 mechanism, they should be flat, because a mission's downstream output should not begin to diverge from its matched comparison missions before the open-data policy that is supposed to cause the divergence. A flat set of leads is necessary but not sufficient for trusting the post-adoption coefficients. Roth demonstrates that a conventional pre-trend test can have low power against the very pre-trends that would most bias the post-treatment estimate, so that an analyst who checks whether the leads are individually insignificant and proceeds is exposed to an undetected violation [\[100\]](#ref-100). The appropriate object is therefore not the binary outcome of the pre-trend test but its power. The plan reports, alongside the leads, the magnitude of a pre-trend that the test would have detected with reasonable probability, so that a flat lead profile is interpreted as ruling out pre-trends of a stated size and not pre-trends of any size. This follows the broader event-study methodology that treats pre-trend testing as a diagnostic with its own error structure rather than as a pass-or-fail gate [\[100\]](#ref-100), [\[133\]](#ref-133)], where [\[133\]](#ref-133) is the regression-imputation benchmarking of parallel-trends violations that situates the size of a tolerable violation against realized data. The step can disqualify a causal reading but cannot, on its own, confirm one: flat, well-powered leads license proceeding to the sensitivity analysis, they do not by themselves establish the effect. It must also survive the objection that any pre-trend test is circular because it uses the same comparison group whose validity is in question. The plan answers this partially through the matched design, which makes the comparison group a like-for-like set rather than an arbitrary one, and concedes that residual circularity is why the Rambachan and Roth sensitivity step follows and does not merely supplement.

### 6.1.7 Step 6: the pre-specified robustness battery

The sixth step re-estimates the event-study path with a robustness battery that was specified in advance, in the shared bible, rather than assembled after the primary result was seen. The battery comprises the Sun and Abraham interaction-weighted estimator [\[113\]](#ref-113), the Borusyak, Jaravel, and Spiess imputation estimator [\[10\]](#ref-10), and the de Chaisemartin and D'Haultfoeuille estimator [\[30\]](#ref-30), each of which targets the same group-time object as the primary estimator but through a different aggregation or weighting scheme. Agreement across this battery is informative because the battery was fixed before estimation. A robustness check chosen after seeing the headline result is a weak signal, since an analyst can select the checks that happen to agree; a battery specified in advance cannot be gamed that way, so concordance across it is evidence and discordance is a flag that demands explanation rather than suppression. The listed estimators coincide with the primary one when its assumptions hold and diverge in interpretable ways when they do not, so that the pattern of agreement is diagnostic of which assumption is binding [\[10\]](#ref-10), [\[30\]](#ref-30), [\[113\]](#ref-113)]. The staggered-DiD methods literature recommends this kind of pre-committed multi-estimator comparison as the standard of practice [\[18\]](#ref-18), [\[35\]](#ref-35)], where [\[18\]](#ref-18) is the applied staggered-DiD tutorial that walks an evaluation through the alternative estimators for a policy effect. The battery probes estimator-driven sensitivity, the sensitivity of the answer to how heterogeneous dynamic effects are aggregated, and not parallel-trends sensitivity, which is the separate province of Step 7; the two must not be conflated. Even a pre-specified battery shares the core identifying assumption, so unanimous agreement across it does not rescue a violated parallel-trends assumption. The plan accepts this and treats the battery as a guard against the aggregation pathology that broke two-way fixed effects, not as a guard against confounding.

### 6.1.8 Step 7: the Rambachan and Roth sensitivity analysis and the robustness region

The seventh step applies the Rambachan and Roth sensitivity analysis [\[97\]](#ref-97) and reports the result as a robustness region rather than as a single point estimate. The analysis asks how large a post-adoption violation of parallel trends, expressed relative to the magnitude of the observed pre-adoption trends, would have to be in order to overturn the estimated effect, and it traces the set of post-adoption violations under which the conclusion still holds. This step converts the binary, low-power pre-trend test into a continuous, interpretable statement about identification robustness. The pre-trend test of Step 5 can fail to detect a trend that nonetheless biases the lags, so the honest object of report is not whether a pre-trend was detected but how robust the conclusion is to plausibly sized undetected trends [\[97\]](#ref-97), [\[100\]](#ref-100)]. Rambachan and Roth establish formally that bounds on the post-treatment trend, anchored to the observed pre-treatment trend, yield identified sets for the treatment effect that can be reported with valid confidence sets [\[97\]](#ref-97). Independent methodological work, including data-driven approaches to control-sample selection and parallel-trends benchmarking, converges on the same principle that parallel trends is a matter of degree to be bounded rather than a binary to be asserted [\[127\]](#ref-127), [\[133\]](#ref-133)], where [\[127\]](#ref-127) is the data-driven control-sample selection method that operationalizes the search for a comparison group under which trends are most nearly parallel. Carried into the decision rule, the robustness region is reported against a pre-stated breakdown threshold, so that the question "does the effect survive" has an answer fixed before the region is computed and not chosen to flatter the result. The step must also survive the point that the anchoring to observed pre-trends is itself a modeling choice. The plan answers by reporting the region across a range of anchoring assumptions and pre-committing to the smallest, most conservative breakdown value as the headline, so that a reader who prefers a stricter anchor finds it already reported. Confidence that this step is the right way to handle the modest-sample, low-power identification problem is high, because the alternative, asserting parallel trends on the strength of an underpowered test, is the practice the cited methodology was developed to replace.

### 6.1.9 Step 8: sensor-class heterogeneity

The eighth step estimates and reports effect heterogeneity by sensor class. The group-time estimator is applied within sensor-class subsets, or equivalently the cohort-time effects are aggregated within sensor class, to produce separate event-study paths for optical imagers, synthetic aperture radar, lidar, passive microwave, and spectrometer missions, subject to the comparison pool being large enough within each class to support estimation. Heterogeneity by sensor class is a substantive object of inference, not a nuisance to be averaged away. The North access-cost mechanism predicts a larger response where a large latent user community is held back only by access cost, and the size of that latent community plausibly varies by sensor class: optical imagery has a broad, cross-disciplinary user base, documented in the Landsat episode, while a specialized passive-microwave or lidar product may serve a smaller community for whom access cost is not the binding constraint [\[77\]](#ref-77), [\[122\]](#ref-122), [\[132\]](#ref-132)], where [\[77\]](#ref-77) is the fifty-year retrospective on Landsat science and impacts. The heterogeneity-robust estimator can report cohort- and group-specific effects natively, without contaminating one subgroup's estimate with another's [\[14\]](#ref-14), [\[113\]](#ref-113)]. Within-class estimation reduces the already modest sample further, so the per-class paths carry wider uncertainty; the plan reports them with explicit precision caveats and does not over-interpret a noisy class-specific null as evidence of no effect in that class. Because sensor class is correlated with mission era and agency, a class-specific effect could reflect an era effect. The plan addresses this through the within-stratum matching that already conditions on age and through reporting whether class-specific effects cluster on particular calendar dates in a way that would signal a confound. The strategic implication of this step is the honest boundary of the contribution's external validity: a result that varies across sensor classes is reported as varying, and the dissertation does not claim a uniform yield of openness across all mission types when its own design is built to detect that it is not uniform.

### 6.1.10 Step 9: the distribution-volume and dataset-citation repeats

The ninth step repeats the core estimation for the two non-primary outcomes, each of which plays a distinct evidentiary role. The distribution-volume outcome, built from Earthdata and DAAC logs, is estimated as an early-response and mechanism check: it sits upstream of publication in the causal chain and should respond to a policy change sooner than publications, which lag by years. The dataset-citation outcome is estimated for the later window only, with explicit power caveats, because formal data citation is sparse early in the observation window and the count is dominated by structural zeros before data-citation practice matured [\[27\]](#ref-27), [\[33\]](#ref-33)]. These two repeats are not redundant robustness on the publication outcome but independent tests of the mechanism and its timing. The North mechanism is a chain, access cost falls, then distribution rises, then impersonal publication rises, then formal dataset citation rises, and a chain can be tested at more than one link [\[85\]](#ref-85). The Kuznets relabeling logic applied to timing supplies the discriminating test: a publication rise accompanied by an antecedent distribution rise is consistent with genuinely new use, whereas a publication rise with no distribution rise is the signature of relabeling, a change in attribution rather than in underlying activity [\[62\]](#ref-62), [\[76\]](#ref-76)]. The distribution outcome is therefore not just a faster version of the publication outcome but a discriminating test between two rival readings of the same publication increase. Distribution logs are an imperfect and partly grey-literature-documented measure whose coverage and definition change across the DAAC system over time, so the distribution result is reported as descriptive corroboration of timing and direction, not as a second independently identified causal estimate. Distribution can also rise for reasons unrelated to research use, for example operational or commercial downloads. The plan concedes this and confines the distribution outcome to its role as a timing-and-direction check on the mechanism rather than as a co-equal outcome.

## 6.2 The fixed decision rule and falsification conditions

### 6.2.1 The rule, carried verbatim

The decision rule that maps the event-study path onto the hypothesis is fixed in advance and reproduced here verbatim from the shared bible, because a rule written after the coefficients are seen is not a rule but a rationalization. Support for H1 requires all three of the following conditions jointly. First, flat leads: the pre-adoption coefficients \(\theta(e < 0)\) are jointly indistinguishable from zero, so that no detectable pre-trend contaminates the post-adoption coefficients. Second, positive lags: the post-adoption coefficients \(\theta(e \geq 0)\) are positive and the aggregated overall effect is positive and statistically distinguishable from zero. Third, robustness: the positive effect survives the Rambachan and Roth sensitivity analysis at the stated breakdown threshold [\[97\]](#ref-97). Failure to reject H0 occurs if the aggregated overall effect is not statistically distinguishable from zero, or if the post-adoption effect does not survive the sensitivity analysis; either outcome falsifies the contribution as stated. There is, in addition, a specific falsifier that is checked first and can halt the causal interpretation before the lags are even examined: positive and trending pre-adoption leads void the parallel-trends assumption, so that the design does not identify the effect, and no causal claim is made regardless of the sign of the lags. And there is a second specific falsifier drawn from the measurement discipline: a publication rise unaccompanied by any distribution rise is read, under the Kuznets logic, as relabeling rather than new use, and also falsifies the contribution even if the publication coefficients are themselves positive and robust [\[62\]](#ref-62), [\[76\]](#ref-76)].

### 6.2.2 Why each condition is a separate gate

The three conjunctive conditions and the two specific falsifiers are not redundant but each guard against a distinct failure mode, so that none can be dropped without reopening a threat. The threat taxonomy of Chapter 5 maps directly onto the rule: the flat-leads condition guards against selection on trends and maturation, the cases where a mission adopts openness precisely when its output was already rising; the positive-and-distinguishable-lags condition guards against a null masquerading as a weak positive; the sensitivity-survival condition guards against an undetected pre-trend of plausible size; the leads-trending falsifier guards against the specific, identification-voiding case where the pre-trend is not merely present but directional; and the publication-without-distribution falsifier guards against the relabeling pathology that the entire Kuznets apparatus exists to catch. Each guard is tied to a published threat: the staggered-DiD literature for the trend and aggregation threats [\[14\]](#ref-14), [\[30\]](#ref-30), [\[35\]](#ref-35), [\[113\]](#ref-113)], the sensitivity literature for the undetected-trend threat [\[97\]](#ref-97), [\[100\]](#ref-100)], and the productivity-measurement literature for the relabeling threat [\[62\]](#ref-62), [\[76\]](#ref-76)]. The rule is conjunctive on purpose, so that the contribution is harder to confirm than to falsify; this asymmetry is deliberate, because a mission-level study that improved on the article-level evidence base only by being easier to confirm would have improved nothing. The rule must survive the point that conjunctive rules can be too demanding, declaring a real effect a null because one underpowered condition failed. The plan answers by separating the inferential conditions, which are frozen, from the reasons a condition might fail, which are reported, so that a failure attributable to power rather than to absence of effect is visible to the reader as such and is carried into the confidence statement rather than silently converted into a claim of no effect. Confidence that the rule correctly operationalizes the hypothesis is high, because each clause is traceable to a specific, pre-stated threat and to a specific element of the estimator and the measurement model.

### 6.2.3 The order of checking and the early halt

The rule is not only a set of conditions but an order of checking, and the order matters. The leads-trending falsifier is evaluated first, before the lags are interpreted, because a directional pre-trend voids identification and renders the sign of the lags causally meaningless; examining the lags first would invite the analyst to read a coincidental post-adoption pattern as an effect when the design cannot support any causal reading at all. This ordering follows again from Roth's pre-test result: the value of the pre-trend check is undermined if it is run after, and conditioned on, the post-treatment estimates [\[100\]](#ref-100). An identification gate must precede the estimate it gates. The early halt is a halt on causal interpretation, not on reporting: a design that fails the leads-trending falsifier still reports its full event-study path, labeled as descriptively suggestive and causally uninterpretable, because suppressing it would itself be a selection on results. The strategic implication is that the dissertation can return an honest "identification failed here" outcome, which is itself a contribution to the literature on when mission-level natural experiments are and are not usable, rather than being forced to manufacture a causal claim from a design that does not support one.

## 6.3 Expected signs and the mechanism reasoning behind them

### 6.3.1 Distribution breaks first and sharper

The first expected sign concerns the distribution-volume outcome, and the expectation is that, if the mechanism operates, distribution volume breaks upward earlier and more sharply than publications. This is an expected sign and a mechanism prediction, not an estimated result. The driver is the open-data policy as an institutional rule change in North's sense [\[85\]](#ref-85). The mechanism is the fall in the transaction cost of obtaining the data: under restricted access a prospective user must locate the data, establish eligibility, negotiate or pay for access, and accept license terms, and under free-and-open release with persistent identifiers and standard licensing those costs fall toward the cost of downloading a file [\[85\]](#ref-85), [\[120\]](#ref-120)]. The observable effect is that the quantity that responds first to a fall in obtaining cost is the act of obtaining itself, the download or distribution event, because it is the most immediate behavior the policy touches. The operational consequence is a break in the distribution series in the adoption period or the period immediately after, sharper than any downstream series because no intervening process, no analysis, no writing, no peer review, separates the policy from the download. The strategic implication is that the distribution series is the cleanest available timing signal for the mechanism, which is why the plan assigns it the mechanism-check role. The strongest empirical anchor for this expected sign is the documented Landsat episode, where the 2008 free-and-open policy was followed by a rise in scene distribution from tens of thousands to tens of millions per year, a step change in the obtaining behavior [\[77\]](#ref-77), [\[122\]](#ref-122), [\[132\]](#ref-132)]. Confidence in the direction of this expected sign is high, anchored to the Landsat benchmark; confidence in its sharpness relative to publications is moderate, because the distribution logs' coverage and definitional consistency across the DAAC system over time are imperfect and could blunt or distort the observed break for measurement rather than behavioral reasons.

### 6.3.2 Publications lag and build

The second expected sign concerns the primary publication-rate outcome, and the expectation is that the publication response lags the distribution response and builds over event time rather than appearing as a single step. This is an expected sign with detailed mechanism reasoning, not an estimate. The driver is again the access-cost fall, but the mechanism now runs through a slow process: a newly enabled user must obtain the data, learn the product, conduct an analysis, write a paper, and pass peer review before a single post-adoption publication is counted, and the median length of that pipeline is measured in years [\[85\]](#ref-85). The observable effect is a publication coefficient path that is near zero in the adoption period, small in the first one or two post-adoption periods, and larger several periods later, the shape the bible's notation \(\theta(e)\) is designed to trace [\[14\]](#ref-14). There is a second, institutional reason for the build, drawn directly from North: communities form around an inherited institutional matrix, and a user community that grew up under restricted access has workflows, intermediaries, and expectations that persist after the rule changes, so the behavioral response is path-dependent and gradual rather than instantaneous [\[85\]](#ref-85). The operational consequence is that a design built to detect this effect must estimate a dynamic path with multiple post-adoption event-time coefficients, which is why a single before-after difference would be the wrong tool and the dynamic event study is the right one. The strategic implication is that the timing of the build is itself a deliverable: it tells NASA and JPL how many periods after a policy change the full scientific yield should be expected to materialize, which matters for evaluating recent policy moves that have not yet had time to show their full effect. Confidence in the direction of this expected sign is moderate to high, because both the pipeline-lag mechanism and the path-dependence mechanism point the same way and the article-level evidence base establishes a positive openness-citation association as the base rate [\[19\]](#ref-19), [\[96\]](#ref-96)]; confidence in the precise rate of build is low, because no mission-level estimate of the build rate exists, which is the gap the dissertation fills.
### 6.3.3 Dataset citation later and lower-powered

The third expected sign concerns the dataset-citation outcome. Any effect on formal dataset-citation rates should appear later than the publication effect and should be estimated with materially lower power. This is an expected sign and a stated power limitation, not an estimate. The driver is twofold: the same access-cost mechanism that drives publications, plus the separate, slower diffusion of formal data-citation practice itself [\[27\]](#ref-27), [\[33\]](#ref-33)]. Formally citing a dataset as a first-class object is a norm that became common only recently, so the dataset-citation count is dominated by structural zeros in the early window regardless of how much the data were actually used. The count can rise both because more researchers use the data and because the practice of formally citing data spreads, and the early window holds too few non-zero observations to separate the two cleanly. The observable effect is a dataset-citation series that is sparse and zero-heavy early and becomes informative only in the later window, which is why the plan restricts this outcome's estimation to the later periods and reports it separately rather than pooling it with publications. The operational consequence is reduced statistical power. Fewer informative observations, more structural zeros, and a shorter usable event-time window all widen the confidence intervals and raise the minimum detectable effect for this outcome relative to the publication outcome. The strategic implication, stated honestly, is that the dataset-citation arm is the weakest of the three and must not be over-interpreted. A null on this outcome is at least as likely to reflect insufficient power as a genuine absence of effect, and the plan pre-commits to reporting it with that caveat attached rather than presenting an underpowered null as evidence for H0. Confidence in the direction of any dataset-citation effect is low, both because of the power limitation and because the practice-diffusion confound is intrinsic to the measure. This low confidence is itself a pre-registered statement, not a result.

### 6.3.4 Larger effect for optical imagers

The fourth expected sign concerns sensor-class heterogeneity. The effect should be larger for optical imagers and smaller or noisier for sensor classes with smaller user communities. This is an expected sign with mechanism reasoning, not an estimate. The driver is the interaction between the access-cost mechanism and the size of the latent user community. The North prediction is that lowering access cost raises use most where a large community was held back only by that cost [\[85\]](#ref-85). Optical imagery serves a broad, cross-disciplinary community (agriculture, forestry, hydrology, urban studies, disaster response) for whom the imagery is directly interpretable and the binding constraint was plausibly access. A specialized sensor class with a small, expert community may instead face a binding constraint of analysis capacity or community size rather than access, so that the same access-cost fall produces a smaller use response. The observable effect is a steeper, more precisely estimated event-study path for the optical class and flatter, wider-interval paths for thin classes. The operational consequence is that the dissertation reports the effect by class rather than averaging across classes, because the average would mislead in both directions: it would understate the optical effect that policy-makers most care about and overstate the effect for classes where access is not the constraint. The strategic implication is the external-validity boundary already stated. The result generalizes within optical remote sensing, where the Landsat evidence shows the mechanism is strong [\[77\]](#ref-77), [\[122\]](#ref-122), [\[132\]](#ref-132)], and is weaker or unestablished where the constraint lies elsewhere. Confidence in the direction of this heterogeneity is moderate, anchored to the Landsat optical evidence on one side but resting on a plausibility argument about community size on the other, with the per-class precision low for thin classes by construction.

## 6.4 Design of the illustrative simulation

### 6.4.1 What the simulation is for and what it is not for

The chapter specifies an illustrative simulation. Its purpose is to demonstrate, on synthetic data with a known data-generating process, that the estimation pipeline recovers the shape of an event-study path that was put into the data by construction, and that the fixed decision rule of Section 6.2 fires correctly on cases built to satisfy H1, to satisfy H0, and to trip each specific falsifier. This simulation validates the procedure; it does not preview the empirical result. A simulation in which the true effect is set by the analyst can only show whether the estimator and rule behave as intended when the truth is known. It says nothing about the unknown real effect, because the real effect is not what was simulated. This is the standard role of a calibration or recovery simulation in econometric practice: a method is validated by confirming it recovers a planted effect and correctly returns a null when none is planted, before it is trusted on real data where the truth is unobserved [\[10\]](#ref-10), [\[14\]](#ref-14)]. Carried as a label on every simulated number, all simulation outputs are illustrative and synthetic. They describe the behavior of the pipeline on data the candidate generated, never the behavior of NASA missions. The simulation must withstand the risk that a reader could mistake a synthetic recovery for an empirical finding. The plan answers by labeling every simulation figure and number as illustrative and synthetic in place, and by reporting the simulation in an appendix clearly separated from the empirical result tables, which remain unpopulated.

### 6.4.2 The synthetic data-generating process

The simulation's data-generating process is specified to mirror the structural features of the real panel that most threaten naive estimation, so that a pass on the synthetic data means something. It generates a synthetic panel of mission-periods with staggered adoption across several cohorts, an unbalanced structure with missions entering and exiting at different periods, a set of never-adopters and not-yet-adopters as comparison units, count-valued outcomes with structural zeros for small and young synthetic missions, over-dispersion in the counts, and a modest number of clusters on the order of tens to match the real sample's small-cluster inference challenge. A synthetic sensor-class covariate and a synthetic mission-age covariate are generated and correlated with the planted effect so that the matching step has work to do. Into this panel the simulation plants a known dynamic treatment effect: a path that is zero in the leads, near zero in the adoption period, and rising over the lags, the shape the publication mechanism predicts. These features, staggered timing, heterogeneity, over-dispersion, structural zeros, and small clusters, are mirrored because each is a feature under which a naive estimator is known to fail. Staggered timing and heterogeneity break two-way fixed effects [\[35\]](#ref-35), over-dispersion and structural zeros break a naive linear-count specification, and small clusters break conventional asymptotic standard errors and motivate the wild-cluster bootstrap. A simulation that omitted these features would validate the pipeline only against an easy case and would give false reassurance about the hard case that the real data present. Even a well-designed synthetic process cannot reproduce every idiosyncrasy of the real bibliographic and access-log data, so simulation success is necessary for trust in the pipeline but not sufficient for trust in the empirical result, which still depends on the identification assumptions holding in the real world.

### 6.4.3 What the simulation demonstrates about the decision rule

The simulation is designed to exercise the decision rule across constructed scenarios, each built to land on a known side of the rule. In the H1 scenario, the planted effect is positive and dynamic with flat leads, and the simulation should show the pipeline recovering flat leads, positive building lags, and an effect that survives the sensitivity analysis, so that the rule returns support for H1 on data where H1 is true by construction. In the H0 scenario, no effect is planted, and the pipeline should return leads and lags both centered on zero and an overall effect indistinguishable from zero, so that the rule returns failure to reject H0 on data where H0 is true by construction. In the leads-trending falsifier scenario, a directional pre-trend is planted with no true treatment effect, and the simulation should show the pipeline detecting the trending leads, the leads-trending falsifier firing, and the early halt on causal interpretation engaging before the lags are read, demonstrating that the rule refuses a causal claim exactly where it should. In the relabeling falsifier scenario, a publication-count rise is planted with no accompanying distribution rise, and the simulation should show the publication-without-distribution falsifier firing, demonstrating that the Kuznets timing logic is operationalized correctly in code. Exercising the rule across these scenarios shows it has the right operating characteristics: it confirms when it should, fails to reject when it should, and refuses a causal reading when identification is voided. A decision rule is only as good as its behavior across the space of cases it must adjudicate, and a rule validated only on the case where it confirms is untrustworthy on the cases where it should refuse, which is the standard logic of testing a classifier against both positive and negative planted cases. Correct rule behavior on synthetic data does not guarantee correct identification on real data, because the real-data threat is a violated assumption the simulation can plant but the real world might hide. The simulation shows the rule works when the truth is known; the empirical caution is that the truth is not known. The operating characteristics described here are illustrative properties of the planned simulation, not measured rejection rates from an executed run.

### 6.4.4 Parameters and reproducibility of the simulation

The simulation's parameters, the number of synthetic missions, the number and timing of adoption cohorts, the count-model dispersion, the planted effect path, the pre-trend slope in the falsifier scenario, and the random seed, are fixed and reported in the pre-registration appendix, so that the synthetic demonstration is itself reproducible. The simulation must meet the same reproducibility standard the dissertation asks of the missions it studies. A non-reproducible simulation is a weak validation, because a reader cannot confirm that the reported operating characteristics follow from the stated process rather than from an unreported tuning. This is the open-data principle the dissertation examines, applied reflexively: the evidence about the pipeline's behavior should be as accessible and reusable as the mission data whose openness is under test [\[27\]](#ref-27), [\[120\]](#ref-120)]. Fixing the seed makes a single run reproducible but does not characterize sampling variability, so the plan specifies repeated runs across seeds to report the distribution of the pipeline's behavior rather than a single realization. The strategic implication is that the simulation appendix doubles as a worked, runnable specification of the entire estimation pipeline, so that the gap between the written plan and the executable analysis is as small as the design stage allows.

## 6.5 Event-study and coefficient-path interpretation conventions

### 6.5.1 Reading the path, not the points

The chapter fixes the conventions by which the event-study path will be read, so that interpretation is governed by rule rather than by the eye. The primary object of interpretation is the path \(\theta(e)\) as a whole, its lead segment and its lag segment, and not any single coefficient in isolation. The joint shape of the path carries the inference; an individual coefficient does not. The hypothesis is about a break and its dynamics, flat before, rising after, and a break is a property of the path's shape, while a single significant or insignificant coefficient at one event time is consistent with many different paths, including paths that do not support H1. This follows event-study methodology in which the leads are tested jointly for pre-trends and the lags are read as a dynamic profile, with the overall aggregated effect summarizing the lag segment [\[14\]](#ref-14), [\[113\]](#ref-113)]. The joint reading is disciplined by the joint pre-trend test and the aggregated effect, both pre-specified, so that "reading the path" does not become an invitation to narrate a noisy figure into a preferred story. Path-reading can be subjective. The plan answers by tying every path-level claim to a pre-specified statistic, the joint lead test, the aggregated lag effect, and the sensitivity region, so that the figure illustrates a conclusion the statistics have already reached rather than substituting for them.

### 6.5.2 The normalization and what it does and does not mean

The convention that the last pre-adoption period \(e = -1\) is normalized to zero is fixed, and its interpretation is fixed with it. The normalization means that every coefficient is read as a difference relative to the immediately pre-adoption period, so the path traces deviations from the eve of adoption. This is a presentational and identification convenience, not a substantive assumption that the effect is zero before adoption. The leads still test for pre-trends despite the normalization, because a non-flat lead segment relative to \(e = -1\) reveals a pre-trend regardless of which period is set to zero. The normalization fixes the reference point; it does not assume away pre-treatment dynamics. This is the standard event-study practice of normalizing to the last pre-period and interpreting leads as a falsification test [\[14\]](#ref-14), [\[113\]](#ref-113)]. One point the plan states explicitly to avoid a common misreading: normalizing \(e = -1\) to zero is not the same as assuming no anticipation, because if missions anticipate the policy and respond before \(e = -1\), the normalization can mask anticipation. The plan therefore reports leads over a window deep enough, \(e = -4\) to \(e = -1\), to detect anticipation as a sloping lead segment rather than hiding it in the reference period. A single normalized reference period could itself be anomalous. The plan addresses this by reporting the path's robustness to alternative normalization periods as part of the pre-specified battery, so that the conclusion does not hinge on the choice of \(e = -1\).

### 6.5.3 Profile interpretation and the aggregated summary

The plan distinguishes two complementary readings of the lag segment: the full dynamic profile and the single aggregated summary effect. The dynamic profile, the sequence of lag coefficients across event time, is the object that locates the effect in time and reveals the build that the publication mechanism predicts. The aggregated summary, a cohort-size-weighted average of the lags, is the object that the decision rule tests for being positive and distinguishable from zero. Both are reported and neither replaces the other. The profile answers "when and how fast" while the summary answers "is there an effect overall," and the dissertation's deliverable to NASA and JPL requires both, the summary for the accept-reject decision and the profile for the timing guidance that tells decision-makers how many periods to wait before a policy's full yield appears. The Callaway and Sant'Anna aggregation scheme derives the summary as a transparent weighting of the group-time effects, so that the summary and the profile are two views of the same underlying estimates rather than separate models [\[14\]](#ref-14). The aggregated summary can conceal heterogeneity across cohorts and across sensor classes, which is why it is always reported alongside the disaggregated profile and the sensor-class-specific paths and never as a stand-alone headline. An aggregated effect could be driven by a single large cohort. The plan answers by reporting the cohort weights and the cohort-specific contributions so that a reader can see whether the summary rests on broad agreement across cohorts or on one influential group.

### 6.5.4 Visualization and tabulation as specified but unpopulated

Finally, the plan fixes the form of the result tables and figures while leaving their cells empty, by design. The event-study table is specified with its columns, event time \(e\), point estimate \(\theta(e)\), confidence interval, for both leads and lags, and with its rows, the event-time index from \(e = -4\) through \(e = +5\), laid out. The sensitivity-region template is specified with its breakdown-threshold axis and its conclusion-status entries laid out. The sensor-class heterogeneity table is specified with one row per class. All of these arrive at the data with their cells blank. A specified-but-unpopulated table is the correct design-stage artifact, and a populated one would be a fabrication. The design-stage discipline is the reason. The estimator, identification strategy, and analysis plan are complete, but no \(\operatorname{ATT}(g,t)\), no event-study coefficient, and no robustness region has been computed on the full assembled panel, so any number in a result cell would be invented [\[14\]](#ref-14), [\[97\]](#ref-97), [\[100\]](#ref-100)]. The pre-registration logic is that the value of fixing the table form in advance comes precisely from leaving the cells empty until the frozen pipeline fills them, because a table whose cells were filled before the pipeline ran would prove the pipeline had been bypassed. The illustrative simulation of Section 6.4 may populate synthetic versions of these table forms, clearly labeled as synthetic, to demonstrate the pipeline's behavior; the empirical versions remain empty. The strategic implication, and the close of the chapter, is that the dissertation's credibility at this stage rests on the discipline of the empty cell. The contribution is the design and its falsification conditions, and the empty result tables are the visible proof that the conclusion has not been written before the evidence has been gathered.

## 6.6 How this chapter advances the argument

This chapter carries the argument forward at the level of procedure. Data-access policy sits on the causal path between a mission and its scientific return, and the Landsat episode shows the mechanism can move usage by orders of magnitude [\[77\]](#ref-77), [\[122\]](#ref-122), [\[132\]](#ref-132)], so the stakes of getting the procedure right are not trivial. The chapter's specific contribution is twofold. The pipeline it fixes estimates the North access-cost mechanism through a matched, staggered event study with distribution logs as an independent upstream timing check [\[14\]](#ref-14), [\[85\]](#ref-85)], and it earns its place over the simpler options by pre-committing to a heterogeneity-robust estimator and a multi-estimator battery in place of the biased two-way fixed-effects default and in place of the article-level association that cannot remove author self-selection [\[30\]](#ref-30), [\[35\]](#ref-35), [\[113\]](#ref-113)]. What the plan cannot guarantee in advance is held in check by stating every expected sign with its confidence grade, by tying every condition of the decision rule to a published threat and its design defense [\[76\]](#ref-76), [\[97\]](#ref-97), [\[100\]](#ref-100)], and by leaving the result tables unpopulated so that no conclusion is asserted ahead of its evidence. The confidence this chapter supports, consistent with the design-stage grade carried throughout, is conditional and moderate at best: the procedure is sound and the rule is well-specified, but whether the real panel will satisfy the rule is unknown and unknowable until the frozen pipeline is run. What would raise that confidence is execution of the pipeline on the assembled panel with flat, well-powered leads and a positive effect that survives the sensitivity region. What would lower it is a trending lead segment, an effect that does not survive the stated breakdown threshold, or a publication rise without a distribution rise. Each of those outcomes is reportable under the plan, and none is foreclosed by it, which is the property a falsifiable design is required to have.

Consistent with the scope decision recorded in Section 2.4, this is an econometric policy-evaluation chapter and does not produce a systems or capability architecture; no system, capability, or data-service exchange is being designed. The plain-language link is restated for completeness: the objective is to maximize the scientific return on NASA's investment in Earth-observation missions, and the decision this analysis informs is whether and when to fund free-and-open data release and the supporting data-system infrastructure at mission formulation. The analysis plan in this chapter is the instrument that turns that objective into evidence, by specifying exactly how the event-study path will be estimated and exactly how it will be read, before the data are seen.
# Chapter 7: Discussion

## 7.0 Overview: both verdicts are informative

This dissertation will return one of two reportable verdicts, and the central claim of this chapter is that both inform NASA and JPL decision-making and that the design has been built so that neither is foreclosed. If H1 is supported, the study delivers a mission-level, identified estimate of the downstream scientific yield of free-and-open Earth-observation data release, located in event time and decomposed by sensor class, converting an asserted benefit into a measured one that can be weighed against the cost of the data-system infrastructure that open release requires. If H0 is not rejected, the study delivers an equally usable finding: that within the population of codable NASA Earth-science missions and the observation window, data-access cost is not the binding constraint on a mission's scientific yield. That finding redirects the recurring investment decision away from access infrastructure and toward analysis funding, product maturity, or community size. The rest of the chapter develops that pair of readings. It interprets the implications under each outcome, returns the result to each anchor framework to say what it would teach about North's access-cost mechanism and Kuznets's proxy-versus-productivity distinction, draws out the policy and mission consequences for the named stakeholders, engages the rival explanations one by one and ties each to the design defense that answers it, states the external-validity boundary honestly, and closes with a calibrated confidence statement that fixes what evidence would raise or lower the reading.

The problem this chapter addresses is the distance between a design that is complete and a contribution that is interpreted. At the close of Chapter 6 the machinery is built, a pre-registered analysis plan with a fixed decision rule and specified-but-unpopulated result templates, but the meaning of each possible result has not been worked out in advance. What is needed is a discussion that has reasoned through, before any estimation, what each verdict implies for theory, for policy, and for the boundary of generalization, so that the reading of the eventual event-study path is itself pre-committed and cannot be retrofitted to whatever the coefficients turn out to be. A discussion written after seeing results is vulnerable to the same specification-search critique that the pre-registration of the design was meant to defeat: a positive result invites a triumphal reading and a null invites an apologetic one, and only a discussion reasoned out at the design stage resists that pull. Left unaddressed, that vulnerability would undo the dissertation's hard-won identification discipline at the last step, with the interpretation doing the work that the estimator refused to let a biased coefficient do. This chapter forecloses it by interpreting both outcomes symmetrically and in advance, holding each to the same evidentiary standard the design holds the estimate to.

Throughout, the epistemic register is the one the bible fixes. This is a design-stage chapter; no \(\operatorname{ATT}(g,t)\), no event-study coefficient \(\theta(e)\), and no robustness region has been computed on the full assembled panel, and every magnitude named here is labeled expected or illustrative. The confidence the design can support is conditional and, at its strongest, moderate, and the chapter states the conditions that would move it in either direction rather than asserting a level the evidence grade cannot bear.

## 7.1 Implications under both outcomes

The design yields a decision-relevant finding regardless of which hypothesis survives, because the two outcomes point to different binding constraints and therefore to different actionable investments. The value of the study is that it can tell those apart rather than presuming the answer.

Consider first the outcome in which H1 is supported: the leads are flat, the post-adoption lags are positive and the aggregated overall effect is positive and statistically distinguishable from zero, and the effect survives the Rambachan and Roth sensitivity analysis at the stated breakdown threshold [\[97\]](#ref-97). The reasons for treating this as the live possibility, rather than a strawman, are the convergent associational evidence assembled in Chapter 3 and the mission-level Landsat precedent: openness is repeatedly correlated with more downstream citation across article-level and dataset-level studies [\[19\]](#ref-19), [\[63\]](#ref-63), [\[96\]](#ref-96)], and the one mission whose free-and-open switch has been studied in depth, Landsat, showed an order-of-magnitude rise in scene distribution and a sharp expansion in publications and operational products after its 2008 policy change [\[77\]](#ref-77), [\[122\]](#ref-122), [\[132\]](#ref-132)]. What lets a confirmed H1 carry a causal reading, where the article-level association cannot, is the identification apparatus: a matched, staggered event study with flat leads and a surviving sensitivity region rules out the secular-trend and selection explanations that the bare correlation leaves open, so a positive lag path is attributable to the policy event rather than to the conditions that accompany it. The magnitude is policy-relevant rather than negligible on the strength of the Landsat record, which makes a proportional increase in the mission-linked publication rate on the order of one quarter to one half by several event-time periods after adoption a plausible illustrative target for a strong-community sensor class, though this is illustrative and not estimated [\[77\]](#ref-77), [\[122\]](#ref-122)]. The effect remains conditional, here as everywhere, on the matched comparison clearing its balance diagnostics and on the sensitivity region not collapsing, and what would defeat the reading is a confirmed pre-trend in the leads, which voids identification before the lags are even examined.

A supported H1 has a specific and unusual property that distinguishes it from a simple "open data is good" conclusion: it locates the effect in event time. The design estimates not a single before-after difference but a dynamic path \(\theta(e)\), and the shape of that path is itself a finding. North's framework predicts a path-dependent, gradual response rather than an instantaneous jump, because a user community that grew up under restricted access has built workflows, intermediaries, and expectations that persist after the rule changes and adjust only over several periods [\[85\]](#ref-85). If the confirmed lag path rises gradually from a small adoption-period effect to a larger effect several periods later, that timing is directly usable: it tells NASA how many periods of post-adoption observation are needed before a recent policy change, such as the Science Mission Directorate Scientific Information Policy, can be fairly evaluated, and it warns against declaring a young open-data policy a failure on the basis of a flat first-year response. The operational consequence is that the study would supply not only a yes-or-no on the benefit but a calendar against which to judge it, which is exactly what a directorate deciding whether to credit or discredit its own policy on the available evidence currently lacks.

Now consider the outcome in which H0 is not rejected: the aggregated overall effect is not statistically distinguishable from zero, or it is distinguishable but does not survive the sensitivity analysis. The reasons for taking this outcome seriously, and not as a mere failure to find what was sought, are twofold. First, the open-access citation-advantage literature is genuinely contested in magnitude: the systematic review by Langham-Putrow and colleagues concludes that while a majority of studies report an advantage, selection effects and field heterogeneity make the size uncertain and some well-identified studies find small or null effects [\[63\]](#ref-63), so a mission-level null is consistent with a real strand of the evidence rather than anomalous. Second, the mission-level treatment is a coarser and later intervention than an author's choice to deposit a dataset, and several plausible mechanisms could blunt it: if the binding constraint on a mission's scientific yield is the funding available to analyze the data, the maturity of the data products, or the sheer size of the relevant research community, then lowering the access cost while those constraints bind would produce little additional downstream use. What lets a non-rejection be read as informative rather than empty is the power analysis fixed in advance in the design: a null in an underpowered design cannot distinguish "no effect" from "an effect too small for this panel to see," but the design commits to a minimum-detectable-effect analysis oriented toward an effect of policy-relevant size, so a null against an adequately powered test in the larger sensor classes does carry the meaning that access cost is not the dominant constraint there [\[83\]](#ref-83), [\[122\]](#ref-122)]. One boundary is sharp: this reading holds only for the arms and strata where power is adequate, and the dataset-citation arm and the thinnest sensor classes are explicitly barred from carrying a null as evidence of no effect because their power is expected to be low.

The asymmetry between the two readings is itself a feature worth stating. A supported H1 is a positive, quantified, time-located benefit estimate. A non-rejected H0 is not a symmetric "open data does nothing" claim; it is the narrower and more careful claim that access cost is not the binding constraint within this sample, which leaves entirely open that open release matters elsewhere, that it has non-scientific benefits the design does not measure (equity of access, operational and societal value), and that the constraint that does bind is separately actionable. The convergence of the FAIR literature on the distinction between nominal and functional openness reinforces this care: a mission coded as open but functionally encumbered, open in license yet practically inaccessible for want of tooling, has not lowered the relevant transaction cost, so a null could in principle reflect treatment that did not treat rather than a mechanism that does not work [\[9\]](#ref-9), [\[120\]](#ref-120)]. The design's reclassification robustness check, which recodes nominally-open-but-encumbered missions, is what lets the study distinguish a true null from a measurement of the wrong thing, and the discussion of any null must report which it found.

## 7.2 Theoretical contribution back to each anchor

Whichever verdict the study returns, it speaks back to its two methodological anchors with a precision that the article-level literature cannot, because the mission-level design tests North's mechanism and honors Kuznets's measurement discipline at the level at which NASA actually sets policy.

Return first to North. The institutional lens supplied the dissertation's mechanism: an open-data policy is a change in the rules of access that lowers the transaction cost of obtaining, verifying, and reusing a mission's data, and lowering that cost should raise the volume of impersonal use by researchers who were not part of the mission team [\[85\]](#ref-85). A supported H1 is direct evidence for this mechanism at the mission scale, and its contribution to the framework is to move the prediction from the abstract to the measured: North's claim that institutions matter because they lower transaction costs is, in this setting, given a number and a time profile. The design's mechanism check also sharpens what counts as evidence for the framework rather than merely consistent with it. The causal chain the bible names runs from the rule change to a fall in transaction cost to a rise in distribution volume first, then to a rise in impersonal publication, then to a rise in formal dataset citation. If distribution breaks earlier and more sharply than publication, as the design expects, the ordering is itself confirmation of the access-cost mechanism specifically, because an access-cost story predicts that the most immediate response is at the point where the cost was lowered, the act of obtaining the data, and only later at the downstream point of publishing with it. This ordering discriminates North's mechanism from rivals because a counting-or-attribution change, the relabeling alternative, would raise publication counts without any corresponding rise in actual downloads, so the observed sequence distribution-then-publication is a signature of new use that a relabeling story cannot produce. This is the contribution back to North: not just that the institution mattered, but evidence on the channel through which it mattered, isolated by the temporal sequence of the proxies.

A non-rejected H0 also speaks to North, and not as a refutation of the framework but as a localization of its scope. North's own account includes path dependence and the inherited institutional matrix: a community formed under restricted access may have built intermediaries and workflows that substitute for open access, so that removing the access barrier changes little because the community had already routed around it [\[85\]](#ref-85). A mission-level null in the larger sensor classes would be consistent with this reading, that the transaction cost the policy lowered was not, in this population, the binding one, because the relevant communities had already absorbed it through intermediaries or because a different cost, analysis or curation, dominated. The contribution to the framework in that case is to identify, in a concrete setting, that the access-cost margin can be slack, which is a refinement North's theory permits and a corrective to a naive reading that any reduction in transaction cost must raise impersonal exchange by a measurable amount. Either verdict, then, returns to North a result the framework can absorb, and the design is what makes the return disciplined rather than rhetorical.

Return now to Kuznets. The measurement lens supplied the dissertation's proxy stance: a citation count is not scientific productivity but a constructed indicator that stands in for it, with a stated and biased error structure, and a rise in the proxy must be shown to be real new output rather than improved counting before it is read as productivity [\[62\]](#ref-62). The contribution back to this anchor is the dissertation's central measurement move, the frozen linkage rule, examined for what it actually accomplishes. McMillan and Rodrik's decomposition of productivity growth into a genuine within-component and a mere reallocation-or-relabeling component is the formal basis for insisting that apparent transformation can be counting rather than output [\[76\]](#ref-76). The analog in this study is exact: after a mission goes open, an apparent rise in mission-linked publications could be real new research or it could be a change in how existing research is attributed and indexed, with more authors now naming the dataset because data-citation norms made the citation easier and expected. By holding the matching rule fixed across the pre- and post-adoption periods, the design forces a change in counting practice to be the same on both sides of the adoption date, so that a measured rise cannot be a counting artifact; and by adding the no-prior-affiliation specification that isolates use by researchers with no prior mission-team tie, it targets North's impersonal use directly. The contribution to the Kuznets tradition is a worked example, at the mission scale, of separating real new output from a relabeling, using a fixed-rule construction and an independent upstream proxy rather than asserting that the count is the truth.

The Kuznets discipline also supplies the standing caution that the chapter must honor in interpreting any positive result: the history of fragile aggregate relationships, in which an empirical pattern that looked robust dissolved once subjected to omitted-variable, trend, and heterogeneity scrutiny, is a warning written into this lineage. The applied-proxy precedent makes the constructive version of the point: Henderson, Storeygard, and Weil treat night-lights as a measurable proxy for economic activity and build a framework that combines the proxy with noisy conventional measures rather than substituting one for the other [\[41\]](#ref-41). The parallel discipline here is that the citation and publication counts are combined with the distribution logs, an independent and upstream proxy, precisely so that no single indicator carries the inference alone, and that the headline is reported as a robustness region under explicit sensitivity analysis rather than as a single point estimate. The contribution to the measurement anchor is therefore not only the frozen-rule construction but the multi-proxy, sensitivity-bounded reporting stance, which is Kuznets's insistence that the construction of an aggregate shapes the inference operationalized into a concrete analytic protocol.

## 7.3 Policy and mission implications for NASA, JPL, and stakeholders

Under either verdict, the study supplies NASA and JPL with a decision input they currently lack: a mission-level, identified basis for the recurring choice of whether and when to fund open-data release and the data-system infrastructure that supports it, replacing an asserted benefit with a measured one or, failing that, redirecting the investment to the constraint that actually binds.

The link between the study's objective and the decision it informs, stated in plain framing terms because the work does not produce a systems or capability architecture, is this. The objective is to maximize the scientific return on the public investment in Earth-science missions. The decision the objective implies, and the one this study informs, is whether and when to fund free-and-open data release and the supporting infrastructure, the Distributed Active Archive Center operation, the curation of products to a reusable standard, and the access tooling, at the point of mission formulation rather than as a retrofit. That decision has real costs, because building and operating a DAAC, curating products, and maintaining access infrastructure are not free, and at present those costs are weighed against a benefit that is asserted at the directorate level and demonstrated only on single before-after episodes with no contemporaneous control. The decision is live and recurring because NASA's Science Mission Directorate has moved deliberately toward free-and-open release and reports annual metrics on the publications, data, and software associated with its funded research, so the agency is already acting on a presumed benefit and already measuring proxies of the kind this study models. An identified mission-level estimate improves the decision, where the directorate-level assertion does not, because the investment is made mission by mission, so a benefit estimated at the mission scale and decomposed by sensor class maps onto the actual decision unit in a way that a directorate-wide average or a single-mission anecdote cannot.

Under a supported H1, the implication is a benefit-cost input with three usable properties. First, it is a magnitude: an estimated proportional increase in downstream publication and, in the later window, dataset-citation yield that can be set against the infrastructure cost, with the proviso that the magnitude is conditional and reported as a region. Second, it is time-located: the event-time path tells decision-makers how long after a formulation-stage open-data commitment the scientific return should be expected to materialize, which bears on how to schedule the evaluation of recent policy and on how to discount a benefit that arrives over several periods rather than at once, consistent with the path-dependent adjustment North predicts [\[85\]](#ref-85). Third, it is heterogeneous by sensor class: the design estimates and reports the effect separately for optical imagers, synthetic aperture radar, lidar, passive microwave, and spectrometers rather than averaging across them, so the benefit-cost case can be made where it is strong and qualified where it is weak. The convergent evidence that Earth-observation data carry first-order, measurable societal and scientific value, from the Landsat distribution and publication record [\[77\]](#ref-77), [\[122\]](#ref-122), [\[132\]](#ref-132)], from the Copernicus user-uptake experience [\[68\]](#ref-68), and from the broader accounting of Earth-observation contributions to sustainable-development objectives [\[131\]](#ref-131), is the backing that makes a positive yield estimate consequential rather than marginal: it places the open-data decision within a domain where the underlying data demonstrably matter, so a positive scientific-yield effect compounds value that is independently established.

Under a non-rejected H0, the implication is not that NASA should stop releasing data openly, and the chapter must guard against that misreading. The narrow, defensible claim is that within this sample access cost is not the binding constraint on scientific yield, which redirects the marginal investment dollar. If access is already cheap enough that lowering it further does not raise downstream use, the binding constraint lies elsewhere, in the funding available to analyze the data, in the maturity of the data products, or in the size of the relevant research community, and each of those is separately actionable: NASA can fund analysis grants, invest in product maturation and analysis-ready data, or invest in community-building and capacity, rather than spending the marginal dollar on access infrastructure whose access-cost margin is slack. The operational consequence is that a null reallocates rather than terminates the investment, and the study's value is in identifying the slack margin so the dollar moves to the binding one. The qualifier that protects this implication is that the study measures scientific yield through bibliometric proxies and distribution logs and does not measure the equity, operational, and societal benefits of open release that exist independently of citation counts, so a null on the scientific-yield margin is silent on those other rationales for open data, which remain in force.

For JPL specifically, the implication tracks the mission-formulation role. JPL designs and operates Earth-science missions and makes the open-data decision at formulation for missions still in development, where the choice can be made deliberately rather than retrofitted. A mission-level yield estimate, located in event time and decomposed by the sensor classes JPL builds, is an input to that formulation-stage decision in a way a directorate average is not, because it can be conditioned on the sensor class and expected user community of the specific mission under design. The honest boundary, carried from the external-validity statement below, is that the estimate is internal to the missions and window observed and transfers most confidently to future missions resembling the strong-community sensor classes that drive the estimated effect, and least confidently to novel sensor classes with small or nascent user communities, where the design's own heterogeneity estimates would counsel caution rather than extrapolation.

## 7.4 Engagement with rival explanations

Every leading rival to the causal reading of a positive result has a corresponding design defense fixed in advance, so that the study does not rest on assuming the rivals away but on a pre-registered procedure that confronts each, and the honesty of the contribution lies in naming the rival that would survive its defense and downgrade the claim.
The first rival is maturation. Missions may produce more publications over time simply because they mature: their data products stabilize, their calibration improves, and their user base grows, all independent of any data-policy change. An apparent post-adoption rise could then be the maturation curve rather than the policy. The mechanism is real and named: mission age drives product stability and community familiarity, which drive downstream use, with no role for the access rule. The design defense is threefold and pre-committed. Mission age enters both as a matching covariate, so a treated mission is compared with restricted-access missions of similar age rather than with the full pool, and as an explicit control, so the maturation trajectory is absorbed rather than attributed to treatment. The flat-leads requirement provides a direct test: if maturation were driving the result, the pre-adoption leads would already be trending upward as the mission matured before adoption, and the falsification rule halts the causal interpretation on exactly that condition [\[14\]](#ref-14), [\[111\]](#ref-111)]. Age controls absorb the average maturation path but not a maturation acceleration that coincides with adoption, which is the second rival.

The second rival is selection on trends, the sharpest threat to the design. Missions may adopt open release precisely when their scientific output is already accelerating. A mission team, anticipating or experiencing a surge in interest, may move to open the data to capitalize on it, so that the policy and the rising output are both caused by a third factor and the policy did not cause the rise. The mechanism is a timing correlation between the adoption decision and an unobserved output acceleration. This rival is why the entire identification apparatus exists. The leads in the event study test directly for pre-adoption divergence, and under valid identification they should be flat. The Roth power diagnostics assess whether the lead test can actually detect a pre-trend of the relevant size, guarding against false reassurance from an underpowered pre-test [\[100\]](#ref-100). The Rambachan and Roth sensitivity analysis is the decisive defense. Rather than asserting that no differential trend exists, it reports how large a post-adoption differential trend, expressed relative to the magnitude of the observed pre-trends, would be required to overturn the estimated effect, so the result is reported as a breakdown region rather than a point that selection could silently move [\[97\]](#ref-97). What makes this an adequate response, short of an experiment, is that it converts an untestable assumption into a quantified robustness statement: the reader is told exactly how much selection-on-trends it would take to explain the result away, and can judge whether a violation of that size is plausible. The candid caveat is this: if the sensitivity region is narrow, a modest and plausible differential trend suffices to overturn the effect, and the study must then report the effect as fragile rather than robust. That is a downgrade the design is built to surface rather than hide.

The third rival is the counting change, the relabeling threat that Kuznets's discipline foregrounds. The apparent post-adoption rise in mission-linked publications could be improved attribution rather than new research. After a mission goes open and data-citation norms spread, existing and continuing research that would have been done anyway is now more likely to name the mission, the instrument, or the dataset, inflating the count without any new use [\[76\]](#ref-76). The mechanism is a change in attribution practice correlated with the policy. The design defense has three parts, each pre-committed. The frozen linkage rule holds the matching procedure fixed across the pre- and post-adoption periods, so a change in how publications name datasets cannot by itself move the count when the rule that detects the naming is the same on both sides [\[27\]](#ref-27), [\[33\]](#ref-33)]. The no-prior-affiliation specification restricts to authors with no prior mission-team tie, isolating impersonal use and excluding the team's own continuing output that is most susceptible to attribution drift. The distribution-log mechanism check is decisive: a relabeling produces more citations without more actual data downloads, so a publication rise unaccompanied by any distribution rise is read, under the falsification rule, as relabeling rather than new use and falsifies the contribution. This triangulation works because the three defenses fail in different ways, so a relabeling would have to defeat all three at once. It would have to evade the frozen rule, occur among authors with no prior affiliation, and somehow coincide with a download surge it did not cause, a far less plausible conjunction than any single counting-change story.

The fourth rival is concurrent policy. A mission's open-data adoption may coincide with a directorate-wide policy change, a new data system, or a broad shift in the publishing or indexing environment, so that the estimated effect captures the common shock rather than the mission-specific rule change. The mechanism is a calendar-time confound shared across missions. The design defense is the matched, contemporaneous comparison group. Because the comparison missions are drawn from the same era and matched on sensor class and age, a common shock that hits all missions at a given calendar time is differenced out, appearing in both the treated and comparison trajectories. The staggered timing is an additional asset here. A true mission-specific policy effect should appear at each cohort's own adoption date in event time, whereas a single directorate-wide shock would cluster on one calendar date across cohorts. The cohort-specific \(\operatorname{ATT}(g,t)\) estimates reveal which pattern holds, and a result that clusters on a single calendar date in a way the event-time alignment cannot explain would signal the confound rather than the policy [\[14\]](#ref-14), [\[35\]](#ref-35)]. One residual remains: a concurrent shock that is itself staggered in lockstep with adoption, for example a data-system rollout sequenced exactly as the open-data adoptions were, would not be differenced out. The hand-coded register's documentation of the surrounding policy and infrastructure context is what lets the study check for and report such a coincidence rather than assume its absence.

Naming the rival that would survive is the honest close of this section. The defenses above are strong against maturation, counting change, and common concurrent shocks, and quantified rather than assumed against selection on trends. The rival that the design cannot fully eliminate is a mission-specific, adoption-synchronized confound: an unobserved factor that affects a single mission's output, is not shared by its matched comparisons, and changes in lockstep with that mission's adoption date. The Rambachan and Roth sensitivity analysis bounds how large such a confound's trend contribution would have to be to overturn the result, but it cannot prove the confound absent. The study's strongest claim is therefore conditional: a positive, robust effect is attributable to the policy unless a mission-specific adoption-synchronized confound of a magnitude the sensitivity analysis reports as implausible is present. That conditional, not an unconditional causal claim, is what the design earns.

## 7.5 External-validity statement

The estimate, if obtained, is internal to NASA Earth-science missions in the observation window. Its generalization is bounded most honestly by the sensor-class heterogeneity the design itself estimates, and the study should report that boundary rather than average it away into a single transferable number.

The basis for a careful external-validity statement is built into the design and the evidence base. The Landsat record establishes that the access-cost mechanism is strong in optical remote sensing, where a large latent user community was held back primarily by access cost and responded to free-and-open release with an order-of-magnitude rise in distribution and a sharp expansion in use [\[77\]](#ref-77), [\[122\]](#ref-122), [\[132\]](#ref-132)]. But Landsat is one sensor class with one unusually large and ready user community, and the mechanism's strength there does not license the assumption that it is equally strong for synthetic aperture radar, passive microwave, lidar, or spectrometer missions whose user communities may be smaller, more specialized, or constrained by analysis capacity rather than access. Reporting heterogeneity rather than a pooled average is the right course because the mechanism itself predicts the effect should scale with the size of the latent user community held back only by access cost. Where the community is large and access is the binding constraint, the effect should be large, as in the Landsat case; where the community is small or the binding constraint is analysis capacity or product maturity rather than access, the effect should be smaller or absent. The design estimates the effect by sensor class precisely so this prediction can be tested and the boundary drawn from the data rather than asserted.

The external-validity boundary therefore has a specific shape. The estimate transfers most confidently to future and out-of-sample missions that resemble the strong-community sensor classes driving any estimated effect, optical imagers above all, and least confidently to novel sensor classes with small or nascent user communities, where the design's own heterogeneity estimates would be noisy and the mechanism's premise of a large latent community held back only by access cost is least likely to hold. Beyond sensor class, three further boundaries apply. The estimate is internal to NASA and may not transfer to other agencies whose missions, communities, and data-system maturity differ; the Copernicus user-uptake experience suggests the mechanism operates in the European context too but under different institutional arrangements that the study does not model [\[68\]](#ref-68). The estimate is internal to Earth-science missions and may not transfer to astrophysics or planetary missions with different community structures and publishing norms. And the estimate is internal to the observation window and a particular publishing and indexing environment; a future environment in which data citation is universal and open release is the default would have a different counterfactual, because the restricted-access comparison that identifies the effect would no longer exist. The honest statement is that the contribution is a conditional, bounded estimate, and that its sensor-class heterogeneity is the primary axis of that boundary, reported as a feature of the finding rather than a limitation to apologize for.

The reciprocal point sharpens the contribution rather than diminishing it. A study that reported a single pooled effect and claimed it for all mission types would be making a stronger claim than its own evidence supports, and the systematic-review literature's central lesson is that field heterogeneity in the open-access advantage is large and that pooled magnitudes mislead [\[63\]](#ref-63). By estimating and reporting heterogeneity, the design refuses that overreach and offers instead a transfer rule: the effect generalizes to the extent that the target mission resembles, in user-community size and binding constraint, the sensor classes for which the effect was estimated. That rule is more useful to a JPL formulation team deciding about a specific future mission than a pooled average would be, because it conditions the transfer on the attributes of the mission actually under design.

## 7.6 Confidence statement

The design supports a conditional, moderate-confidence reading at its strongest. The confidence is calibrated to the design-stage evidence grade rather than to the appeal of the hypothesis, and the conditions that would raise or lower the confidence are stated in advance so that the eventual estimate is read against a fixed standard.

The reasons for capping the confidence at moderate, even for a supported H1, are three structural features named throughout the design. First, the number of distinct Earth-science missions with codable access regimes is on the order of tens, not hundreds, so the inference rests on a modest number of clusters, the matching pool for some sensor classes is thin, and the wild-cluster bootstrap intervals are correspondingly wide; small-cohort inference is a standing limit on how strong any claim can be [\[14\]](#ref-14). Second, the outcome is a constructed proxy with a biased error structure, right-skewed, lagged, dependent on field size and citation norms, and sensitive to indexing coverage, so even a clean estimate is an estimate of a proxy for productivity rather than of productivity itself, and the Kuznets discipline forbids treating the proxy as the latent quantity [\[62\]](#ref-62). Third, identification rests on a conditional parallel-trends assumption that is supported by flat leads and bounded by sensitivity analysis but cannot be proven, so the strongest causal claim is conditional on the sensitivity region being wide enough that a plausible confound cannot overturn the effect [\[97\]](#ref-97). Confidence is stated as a calibrated level rather than asserted as significance because the evidence grade at the design stage is a complete and pre-registered plan, not an executed result. No level above moderate is honestly available, and even moderate is contingent on the estimation clearing its own diagnostics.

The conditions that would raise confidence are specific and worth fixing now. Confidence rises if the matched comparison clears its balance diagnostics cleanly, so that the parallel-trends premise is well supported within strata; if the leads are flat under an adequately powered lead test, so that selection on trends is not merely undetected but detectably absent; if the effect survives a wide Rambachan and Roth breakdown region, so that only an implausibly large confound could overturn it; if the headline agrees across the pre-specified robustness estimators, so that the result is not an artifact of one method's weighting [\[10\]](#ref-10), [\[30\]](#ref-30), [\[113\]](#ref-113)]; and, most distinctively, if the distribution logs break earlier and more sharply than the publication counts, because that ordering is the mechanism signature that upgrades the claim from a correlation consistent with North's framework to evidence for the access-cost channel specifically. The conditions that would lower confidence are the mirror image: imbalance that the matching cannot resolve, leads that trend, a narrow sensitivity region that a modest confound defeats, disagreement across estimators, or a publication rise with no distribution rise, the last of which does not merely lower confidence but triggers the relabeling falsifier and overturns the contribution outright.

The confidence statement applies asymmetrically across the three outcome arms, as the power analysis requires. The distribution-volume arm is expected to be the best powered and the earliest to respond, so a clear result there carries the most weight and the mechanism reading rests on it. The publication arm is the headline and is expected to be adequately powered in the larger sensor classes and marginal in the thin ones, so its confidence is conditioned on sensor class. The dataset-citation arm is the weakest, because formal data citation is sparse in the early window and the panel is short, so it is reported as exploratory, is barred from carrying the headline, and a null on that arm is explicitly refused as evidence of no effect [\[27\]](#ref-27), [\[33\]](#ref-33)]. This per-arm calibration is the honest alternative to a single confidence figure that would over-credit the weakest arm or under-credit the strongest.

The closing position is the one the argument has carried since Chapter 5 and which this chapter now states for the interpretation rather than the design. High confidence is warranted that the estimator and identification strategy are the correct ones for this data structure, because the staggered timing and heterogeneous, dynamic effects are exactly the conditions under which the Callaway and Sant'Anna apparatus is appropriate and the naive two-way fixed-effects estimator is not [\[14\]](#ref-14), [\[35\]](#ref-35)]. Moderate confidence is the ceiling for the substantive reading of any estimate, conditional on the diagnostics above. Low confidence attaches to transfer beyond the strong-community sensor classes. And the design's deepest commitment, that both a positive and a null result are reportable and that neither is foreclosed by the specification, is what makes the confidence statement credible rather than self-serving. A study that could only confirm its hypothesis would deserve no confidence at all, and it is precisely because this design can falsify its own contribution, on a rule fixed before estimation, that a supported H1 would earn the moderate confidence claimed and a non-rejected H0 would earn the redirected-investment reading rather than an apology.

## 7.7 Chapter synthesis: the interpretation pre-committed

This chapter has carried the dissertation's argument into the interpretive register, settling in advance what each verdict means so that the reading of the eventual event-study path is fixed rather than retrofitted. The earlier chapters established that the question matters, drawing on the convergent associational evidence and the Landsat record [\[19\]](#ref-19), [\[68\]](#ref-68), [\[77\]](#ref-77), [\[96\]](#ref-96), [\[122\]](#ref-122), [\[131\]](#ref-131), [\[132\]](#ref-132)]. This chapter has shown that the design speaks specifically to North's access-cost channel, isolated by the distribution-then-publication sequence, and honors Kuznets's proxy discipline through the frozen rule and multi-proxy reporting [\[41\]](#ref-41), [\[62\]](#ref-62), [\[76\]](#ref-76), [\[85\]](#ref-85)]. Its edge over simpler alternatives is re-secured here against each rival explanation by name, with maturation, counting change, and common shocks defended by pre-committed procedure and selection on trends bounded by quantified sensitivity rather than assumed away [\[14\]](#ref-14), [\[35\]](#ref-35), [\[97\]](#ref-97), [\[100\]](#ref-100), [\[111\]](#ref-111)]. What remains uncertain is held within bounds by the candid external-validity boundary drawn along sensor-class heterogeneity and by the calibrated, per-arm confidence statement that caps the substantive reading at moderate and names the conditions that would move it [\[10\]](#ref-10), [\[27\]](#ref-27), [\[34\]](#ref-34), [\[63\]](#ref-63)].

What this chapter does not do, and does not claim to do, is report a result. No coefficient has been estimated, no robustness region computed, and no rival empirically adjudicated on the assembled panel; every magnitude named here is illustrative or expected, and every interpretation is a conditional reading of a result that does not yet exist. The contribution of the chapter is to have made those readings symmetric and pre-committed, so that whichever verdict the estimation returns, a mission-level identified yield estimate usable in formulation-stage data-policy decisions if H1 holds, or a localization of the binding constraint away from access cost if H0 is not rejected, is interpreted against a standard fixed before the data were seen. Chapter 8 restates the contribution that stands regardless of the sign of the effect, states the limitations honestly, and sets out the concrete program of assembling the panel and executing the pre-registered pipeline on which H1 will finally be supported or falsified.


# Chapter 8: Conclusion

## 8.0 Overview: the contribution restated

The central claim of this concluding chapter is that the dissertation delivers a durable contribution whose value does not depend on the sign of the effect it is designed to estimate. The deliverable is a mission-level, matched, staggered-adoption difference-in-differences design, together with a frozen measurement protocol and an assembled register of open-data-policy adoption dates, that can either support or falsify a single pre-registered hypothesis pair about the downstream scientific yield of free-and-open Earth-observation data release. Whether the executed event study eventually supports H1, the alternative that open-data adoption produces a measurable upward break in a mission's publication and dataset-citation yield, or fails to reject H0, the null of no effect, the apparatus that produces that answer is itself the principal scientific product. A design built so that both outcomes are reportable, and neither is foreclosed by the specification, is worth more to NASA and to the Jet Propulsion Laboratory than a single point estimate produced by a design that could only ever return one sign. This chapter develops that claim, states the limitations honestly, lays out a concrete program for executing the design on the full data and extending it, and closes on the reflexive point that the reproducibility of this study is itself an application of the open-data principle it puts under test.

The problem this chapter addresses is one of disposition. At the close of the design work, a complete estimator, a complete identification strategy, and a complete pre-registered analysis plan all sit upstream of an unexecuted panel. What the conclusion owes the reader is a clear account of what the dissertation has already established, what remains contingent on execution, and what should be done next, written so that a reader who reaches the end can distinguish the settled from the provisional without re-reading the methods. The standing temptation, in a design-stage dissertation, is to let the asserted promise of the future result quietly stand in for a contribution, so that the work is defended on what it might find rather than on what it has built. Yield to it and the falsifiability of the contribution, which is its chief methodological virtue, gets read as a weakness, as if a design that can return a null were a design that has failed. This chapter resists that pull by separating the contribution that is already in hand from the estimate that is not, and by showing that the former is the load-bearing one.

## 8.1 The contribution, and what stands even if H1 is not confirmed
The dissertation makes one falsifiable contribution, stated throughout as a hypothesis pair on the mission as the unit of analysis. H0 holds that the transition to free-and-open data release has no effect on a mission's downstream peer-reviewed publication rate or its dataset-citation rate, relative to matched restricted-access missions. H1 holds that the transition produces a measurable upward break, an increase in level or slope, in those yields relative to matched restricted-access missions, in the periods after adoption. The claim is falsifiable in both directions, and the decision rule that adjudicates it was fixed before any estimation: support for H1 requires flat pre-adoption leads, positive post-adoption lags with a positive and statistically distinguishable aggregated effect, and survival of that effect under the Rambachan and Roth sensitivity analysis [\[97\]](#ref-97) at a stated breakdown threshold. The disposition claim precedes the hypothesis here for a reason. The hypothesis is the part of the work that remains open, while the design that will close it is already finished.

Three components of the dissertation stand as contributions regardless of whether the executed event study supports H1 or fails to reject H0. They are worth naming precisely, because the case that the contribution survives a null rests on them.

The first is the mission-level design itself. The open-data-advantage literature is conducted overwhelmingly at the level of the individual article or dataset, where the treatment is an author's choice and the central threat is self-selection: better research, or research by better-resourced groups, may be both more likely to be made open and more likely to be cited [\[63\]](#ref-63). Piwowar and Vision [\[96\]](#ref-96) and Colavizza and colleagues [\[19\]](#ref-19) establish the associational base rate at that level, and Langham-Putrow and colleagues [\[63\]](#ref-63) establish that the magnitude is contested precisely because selection is pervasive. This dissertation moves the unit of analysis from the self-selecting article to the mission, where the treatment is a policy event rather than an author choice, and exploits the staggered timing of open-data adoption across NASA Earth-science missions as a natural experiment that modern heterogeneity-robust difference-in-differences methods have not previously been applied to. This reframing is a contribution whatever the executed result. It supplies the field with a unit of analysis at which the policy lever NASA actually pulls, mission-level or directorate-level data policy, can be evaluated, and it converts the single before-and-after Landsat episode [\[122\]](#ref-122), [\[132\]](#ref-132)] into one cohort within a multi-mission, matched, contemporaneously-controlled design. A null result obtained from this design would be a more informative null than any the article-level literature can produce, because it would be a null on an identified estimand rather than a wash of conflicting associations. The mechanism that motivates the design is North's: an open-data policy is an institutional rule change that lowers the transaction cost of obtaining and reusing mission data and should, if the framework holds, raise impersonal downstream use [\[85\]](#ref-85). The design operationalizes that mechanism into a testable dynamic path; the path is the contribution even before the data populate it.

The second is the frozen measurement discipline. Following Kuznets and the national-accounts tradition, the dissertation treats the citation and publication counts as constructed proxies for the latent quantity of scientific productivity, not as that quantity itself, and it states the proxy's known biases before any inference: right-skew, citation lag, dependence on field size and citation norms, and sensitivity to indexing coverage in the source database [\[62\]](#ref-62). This discipline operates through a rule. The bibliographic matching procedure, by which a publication is linked to a mission through mission and instrument name matching, dataset-identifier matching, and acknowledgment-text matching, is held fixed across the pre- and post-adoption periods, so that a change in counting practice cannot masquerade as a change in output. This frozen-rule protocol, reinforced by a supplementary specification that restricts to authors with no prior mission-team affiliation to isolate impersonal use in North's sense, and by the use of Earthdata and Distributed Active Archive Center distribution logs as an independent upstream mechanism check, is a transferable methodological contribution. It is the concrete instrument by which the McMillan and Rodrik distinction between a real change in output and a relabeling [\[76\]](#ref-76) is enforced in a bibliometric setting. The discipline stands whatever the sign of the effect, because it is a protocol for honest measurement that other mission-level bibliometric evaluations can adopt directly, and because it is precisely the protocol that lets a measured rise be defended as new use rather than improved attribution.

The third is the assembled adoption register. A hand-coded, double-entered, adjudicated register that records, for each codable NASA Earth-science mission, the date of transition to free-and-open release, the prior access regime, and the licensing and tooling status before and after, with phased and ambiguous transitions flagged, is a research asset in its own right. It does not exist in the prior literature, where the Landsat date is treated as a single well-documented episode rather than as one entry in a structured cross-mission table. The register, built against mission documentation, DAAC policy records, and the directorate's Scientific Information Policy and its implementation metrics, is a contribution that survives any estimation outcome because it enables every future study that wants to treat mission data policy as a structured variable, not only the difference-in-differences study designed here. The register also encodes, through its phased-transition flags and its nominal-versus-functional distinction drawn from the FAIR vocabulary [\[120\]](#ref-120), a coding judgment that other investigators can inspect, contest, and reuse.

What ties these three components to the disposition is a principle central to credible empirical work: the value of a research design lies in its capacity to discriminate between hypotheses, not in the direction of the answer it happens to return. The pre-registration literature insists that a design specified to be falsifiable in advance produces evidence that is informative whichever way it falls, because the informativeness is purchased by the prior commitment, not by the realized sign [\[97\]](#ref-97), [\[100\]](#ref-100)]. One distinction is protected here: the contribution stands as a design and a set of assets, at design-stage confidence; it does not yet stand as an estimate, and no estimated \(\operatorname{ATT}(g,t)\), event-study coefficient \(\theta(e)\), or robustness region is claimed as a finding anywhere in this dissertation. A reader might object that a design with no executed result is merely a promissory note. The response is that the three named components, the mission-level estimand, the frozen-rule protocol, and the adoption register, are each usable now, independent of execution, by NASA, JPL, and other investigators, which is the operational test of whether something is a contribution rather than a promise. Confidence in this disposition claim is high, because it rests on assets that already exist rather than on a result that does not.

## 8.2 Limitations, stated honestly

The strength of any claim this dissertation eventually makes is bounded by the weakest of its data and design constraints, not the strongest, and the honest course is to state those constraints plainly here so that a reader weights the executed result accordingly. Five limitations carry from the data and design chapters into this conclusion, and each is paired with the mitigation built into the analysis plan rather than waved away.

The first and most consequential is the small cohort. The number of distinct NASA Earth-science missions with a clearly codable access regime and adoption date is modest, on the order of tens rather than hundreds, so the design is more vulnerable to small-sample inference problems than the article-level studies it improves upon, and the matching pool for some sensor classes may be thin. This is a real constraint on statistical-conclusion validity, and no better estimator can engineer it away, because the binding limit is the count of treated and comparison units the world actually provides. The mitigation is to use wild-cluster bootstrap inference rather than conventional asymptotics, to prefer the heterogeneity-robust estimators of Callaway and Sant'Anna [\[14\]](#ref-14), Sun and Abraham [\[113\]](#ref-113), and Borusyak, Jaravel, and Spiess [\[10\]](#ref-10) over the naive two-way fixed-effects estimator that Goodman-Bacon [\[35\]](#ref-35) shows to be unreliable under staggered timing, and to report the dataset-citation arm with explicit power caveats. The honest statement is that with tens of missions the design may lack the power to distinguish a small true effect from zero, so a failure to reject H0 must itself be read with care: it could reflect a genuine absence of effect, or it could reflect insufficient power to detect a present one. The minimum-detectable-effect analysis specified in the design chapter exists precisely so that this ambiguity can be quantified rather than ignored.

The second is imperfect bibliographic linkage. Linking a publication to a specific mission is itself an error-prone operation, because authors name missions, instruments, and datasets inconsistently, so the linkage rule introduces measurement error. The threat is not the existence of that error but its possible correlation with the treatment: if the propensity to name a mission changed around the time of open release, for example because data-citation norms strengthened and authors began naming datasets more readily [\[27\]](#ref-27), [\[33\]](#ref-33)], then a change in linkage could be confounded with the policy effect. The primary defense is the frozen matching rule, which holds the linkage procedure constant across periods so that any change in counting reflects a change in underlying use rather than a change in the instrument. The secondary defense is the no-prior-affiliation specification, which isolates impersonal use and is less exposed to within-team attribution drift. The honest residual is that freezing the rule controls a change in the rule, not a change in author behavior under a fixed rule; the distribution-log mechanism check is the independent line of evidence that guards against reading a pure attribution shift as new use.

The third is sparse early data citation. Formal citation of datasets as first-class objects became common only recently, so the dataset-citation outcome is available only for the later part of the observation window and is analyzed separately rather than pooled with publication counts. This restricts the statistical power of the dataset-citation arm and means that the cleanest expression of the North mechanism, formal acknowledgment of reuse, is the outcome with the least data behind it. The mitigation is to carry the power caveat explicitly into every report of that arm and to lean on the publication-rate and distribution-volume outcomes, which have longer histories, for the primary inference. The honest statement is that the dissertation should not, and by design does not, rest its conclusion on the dataset-citation outcome alone.

The fourth is phased adoption. For some missions the transition to free-and-open release is a process rather than a clean event, with license, tooling, and access changing on different dates, so the single adoption date that the event study requires is a coding simplification of a more gradual reality. The mitigation is to flag phased transitions in the register and to test sensitivity to alternative date definitions, treating the choice of date as a robustness dimension rather than a fixed input. The honest residual is that a smeared treatment will tend to attenuate the estimated break, biasing the design toward a null, so a positive result obtained despite phased adoptions is conservative, while a null obtained in their presence is harder to interpret.

The fifth, and the one the framework itself foregrounds, is the proxy character of the outcome. A citation count is not scientific productivity; it is a constructed indicator that stands in for it, with a biased error structure [\[62\]](#ref-62). The night-lights tradition supplies the disciplined stance: a satellite-derived proxy can be combined with noisy direct measures to learn about a latent quantity, but it must not be asserted to be that quantity [\[41\]](#ref-41). The mitigation is the entire Kuznets apparatus of this dissertation, the stated error structure, the dual-source design across the NASA Astrophysics Data System [\[60\]](#ref-60) and Web of Science to catch single-database indexing artifacts, the frozen counting rule, and the relabeling check. The honest statement is that even a clean, well-identified event-study path estimates an effect on the proxy, and the inference from the proxy to scientific productivity itself remains a construct-validity argument, made as strong as the design can make it but not eliminated by it.

What links these five limitations to the disposition of the dissertation is the construct-validity principle that an estimate is only as informative as the weakest link in the chain from concept to measure to design. The distinction protected throughout is that these limitations bound the eventual executed claim; they do not undermine the three design-stage contributions of Section 8.1, which are assets independent of any estimate. Confidence that the limitations have been stated completely is moderate-to-high: they are the five carried forward from the prospectus and the data chapter, each tied to a specific mitigation, but a design not yet executed may surface limitations that only the data reveal, which is itself an argument for the execution program that follows.

## 8.3 A concrete future-research program

The thesis of this section is that the path from the present design-stage dissertation to an executed, reported result is specific, sequenced, and tractable, and that a small set of well-defined extensions then widens the contribution beyond NASA Earth-science missions without abandoning the identification logic that makes the core design credible. The program is stated as a pipeline, not a wish list, so that a successor investigator can begin at step one rather than reconstruct the plan.

### 8.3.1 Executing the design on the full data

The immediate next step is to execute the pre-registered analysis pipeline on the full assembled panel. The sequence is fixed and was specified before any estimation, to forestall the specification search that would otherwise let the analyst tune the design toward a preferred sign. First, assemble the mission-period panel by linking the NASA Astrophysics Data System [\[60\]](#ref-60) and Web of Science publication and citation records to each mission, merging the Earthdata and DAAC distribution logs, and attaching the hand-coded adoption date and prior access regime from the register. Second, construct the three outcomes, publication rate, dataset-citation rate, and distribution volume, and the matching covariates, sensor class and mission age, using the frozen matching rule so that counting practice is held constant across the pre- and post-adoption periods. Third, match restricted-access comparison missions to open-access treated missions on sensor class and mission age using the propensity-score framework of Rosenbaum and Rubin [\[99\]](#ref-99) and the matching guidance of Stuart [\[111\]](#ref-111), and report covariate balance with the standardized-difference diagnostics of Austin [\[8\]](#ref-8), proceeding only if balance is acceptable. Fourth, estimate the dynamic event-study path \(\theta(e)\) with the Callaway and Sant'Anna group-time estimator [\[14\]](#ref-14), normalizing the last pre-adoption period to zero. Fifth, test the leads for pre-trends and apply the Roth power diagnostics [\[100\]](#ref-100) to assess whether the pre-trend test is powered to catch a violation. Sixth, re-estimate with the Sun and Abraham [\[113\]](#ref-113), Borusyak, Jaravel, and Spiess [\[10\]](#ref-10), and de Chaisemartin and D'Haultfoeuille [\[30\]](#ref-30) estimators as a pre-specified robustness battery. Seventh, apply the Rambachan and Roth sensitivity analysis [\[97\]](#ref-97) and report the robustness region, expressing how large a post-adoption differential trend would be required to overturn the estimated effect. Eighth, estimate and report effect heterogeneity by sensor class. Ninth, repeat the core estimation for the distribution-volume outcome as an early-response and mechanism check and for the dataset-citation outcome with explicit power caveats. The decision rule is then read off the path under the fixed conditions: flat leads, positive lags with a positive distinguishable aggregate, and survival under sensitivity. This is not new design work; it is the execution of design work already complete, and that is exactly why it is the first item in the program.

The mechanism reasoning that the executed pipeline is built to test should be restated so the successor knows what observable pattern would corroborate it and what would not. Free-and-open release, as an institutional rule change in North's sense [\[85\]](#ref-85), lowers the transaction cost of obtaining, verifying, and reusing the data toward the cost of a download. The first observable consequence is that distribution and download volume rise, which the Earthdata and DAAC logs capture upstream of any publication. The next consequence is that impersonal downstream use by non-team researchers rises, captured by the publication rate, and, in the later window, by formal dataset citation. The operational consequence for NASA and JPL is that the cost of open-release infrastructure can be weighed against a measured rather than asserted yield, located in event time and decomposed by sensor class. The pattern that corroborates this causal reading is a distribution break that precedes and is sharper than the publication break, with flat leads on both; a publication rise unaccompanied by any distribution rise would, under the Kuznets discipline, be read as relabeling rather than new use, and would falsify the mechanism even if the publication coefficients were positive. The successor must therefore treat the distribution-log result as load-bearing, not decorative, because it is the line of evidence that separates the causal mechanism from a counting artifact. Where only correlation is available, the successor must say so and downgrade confidence accordingly; the upgrade from the article-level associational base rate [\[19\]](#ref-19), [\[96\]](#ref-96)] to a conditional causal reading is earned only by flat leads and a surviving sensitivity region, and only conditionally.

### 8.3.2 Extending beyond NASA Earth-science missions

Once the core design is executed and its sensor-class heterogeneity reported, three extensions widen the contribution without abandoning the identification logic. The first is to extend the unit set beyond NASA Earth-science missions to non-NASA agencies operating comparable Earth-observation programs, most obviously the Copernicus program, whose user-uptake trajectory [\[68\]](#ref-68) offers a second large mission-level natural experiment in a different institutional setting. Cross-agency replication tests the external-validity boundary directly: if the access-cost mechanism is general, the matched event study should recover a comparable dynamic path in a program that adopted open release under a different policy architecture. The honest caution is that cross-agency comparison introduces new confounders, different funding environments, different user communities, different indexing coverage, so the extension must re-run the full matching and sensitivity machinery rather than assume transportability. The Landsat and Copernicus precedents [\[122\]](#ref-122), [\[132\]](#ref-132)] together suggest the mechanism is strong in optical remote sensing with a large latent user community; the extension is where that suggestion is tested rather than asserted.

The second extension is to non-Earth missions within NASA, for which the NASA Astrophysics Data System provides comparable bibliographic linkage [\[60\]](#ref-60). Astrophysics and planetary missions adopt data-release policies on their own timelines, and the same staggered-adoption logic applies. The scientific interest is in whether the access-cost mechanism, which the Earth-science design isolates, operates with similar magnitude where the user community, the data-product structure, and the analysis-capacity constraint differ. This extension also stress-tests the proxy: citation norms differ across subfields, and a mechanism that holds for Earth-observation publications need not hold where the binding constraint is analysis capacity or community size rather than access cost. The honest framing, carried from the discussion, is that sensor-class heterogeneity within the Earth-science sample is the first signal of where the effect travels and where it does not, and the non-Earth extension is the natural test of that boundary.

The third extension is forward-looking rather than retrospective: to embed the open-data decision in future missions at formulation, so that the policy choice is made deliberately and prospectively rather than studied after the fact. The retrospective design estimates the effect of policies already adopted under whatever incidental timing the historical record provides. A prospective design, in which a future Earth-science mission's open-data decision and its supporting data-system investment are specified at formulation with measurement of downstream yield planned in advance, would convert the natural experiment into something closer to a designed one, with cleaner treatment timing and pre-committed outcome measurement. This is the point at which the dissertation's plain-language link between objective and decision becomes operational: the objective is to maximize the scientific return on Earth-mission investment, and the decision the estimate informs is whether and when to fund open-data release and the supporting data-system infrastructure at mission formulation. Stating that link in plain language is deliberate; this is an econometric policy-evaluation contribution, and it does not produce a systems or capability architecture.

The reason for sequencing the program this way, execute first, then extend across agencies, then across mission types, then forward into formulation, is that each step reuses the identification machinery validated by the prior step, so that credibility accumulates rather than being re-argued from scratch at each extension. Every extension re-incurs the matching and sensitivity burden in its new setting and must report it; transportability is a hypothesis to be tested, not an assumption to be inherited. Confidence that the execution step is tractable is high, because the pipeline is fully specified and the data sources are real and accessible; confidence that the extensions will recover comparable effects is, appropriately, only moderate at design-stage, contingent on the core result and on the new settings' confounders.

## 8.4 Closing: reproducibility as the principle under test
The closing thesis is reflexive, and it states most plainly what this dissertation is about. The study asks whether making mission data free, open, and reusable raises the downstream scientific yield of a mission. The evidence the study produces for or against that proposition should itself be as free, open, and reusable as the mission data whose openness is under test. This is not a rhetorical flourish. It is a methodological commitment that the design enforces. The analysis code, the hand-coded adoption-date register with its sources and its phased-transition flags, and the bibliographic linkage rules are intended for release, so that an independent investigator can reconstruct the mission-period panel and reproduce the event-study path. The outcome definitions, the matching procedure, the primary and robustness estimators, the event-time window, the clustering level, and the decision rule are all pre-registered and fixed before estimation. That prior commitment, rather than the realized sign, is what makes the eventual result informative whichever way it falls.

The deeper point is that reproducibility is the institutional mechanism the dissertation studies, turned on the dissertation itself. North's framework holds that an open rule lowers the transaction cost of impersonal use and thereby raises that use [\[85\]](#ref-85); a reproducible, pre-registered study lowers the transaction cost for an independent researcher to verify, contest, and build on the result, and so raises the impersonal scientific use of the study's own output. Kuznets's discipline holds that a constructed proxy must travel with its stated error structure or it will mislead [\[62\]](#ref-62); an openly released register and codebook let others inspect, recompute, and challenge the proxy's construction rather than accept it on assertion. The study practices what it estimates. If the executed event study supports H1, the dissertation will have shown, at the mission level and with an identified design, that lowering the cost of access raises downstream scientific use, and it will have done so through an artifact that itself lowers the cost of access to its own evidence. If the executed study fails to reject H0, the dissertation will have shown, through the same open and reproducible machinery, that within this sample the binding constraint on a mission's scientific yield lies elsewhere: in analysis funding, in data-product maturity, or in community size. That finding will be as openly contestable as the data policy it concerns.

Either way, the contribution that closes this dissertation is the one it opened with: a falsifiable, mission-level design, a frozen measurement discipline, and an assembled adoption register, built so that both answers are reportable and neither is foreclosed, and released so that the evidence is as open as the policy it examines. The numbers in this dissertation are illustrative and design-stage. They have not been executed on the full assembled panel, and no estimated coefficient is reported as a finding. What is finished is the apparatus that will produce the answer, and what is reflexively consistent is the commitment to produce that answer in the open. The next investigator to take up this work will not have to ask what to do. They will assemble the panel, run the pipeline in the design, and report the event-study path and its sensitivity, after which H1 will be either supported or falsified on the stated decision rule, in public, on data and code that others can reuse. That is the proper close for a study of open data: not a claim, but a reproducible method for earning one, offered in the same spirit of stewardship and service that a public investment in observing the Earth is meant to honor, and left open so that those who come after may verify it, contest it, and build upon it.
# References

## Prospectus seed-number crosswalk

Every in-text citation in this document resolves directly to its entry in the full author-sorted reference list below, rendered as a clickable [\[N\]](#ref-N) marker. The table below is retained for provenance only: it records how the twenty-six prospectus seed references, originally numbered [1] through [26] in the design prospectus, map onto their entries in the unified author-sorted list, so that a reader holding the prospectus can trace each seed source forward. The crosswalk is a navigational aid; the authoritative bibliographic detail for every source is its full entry in the list below.

| Prospectus [N] | Author (year) | Master entry |
|---|---|---|
| [1] | Piwowar and Vision (2013) | 96 |
| [2] | Colavizza et al. (2020) | 19 |
| [3] | Eysenbach (2006) | 32 |
| [4] | Gargouri et al. (2010) | 34 |
| [5] | Langham-Putrow et al. (2021) | 63 |
| [6] | McKiernan et al. (2016) | 75 |
| [7] | Wulder et al. (2019) | 122 |
| [8] | Zhu et al. (2019) | 132 |
| [9] | Wilkinson et al. (2016) | 120 |
| [10] | Data Citation Synthesis Group (2014) | 27 |
| [11] | Fenner et al. (2019) | 33 |
| [12] | Callaway and Sant'Anna (2021) | 14 |
| [13] | Goodman-Bacon (2021) | 35 |
| [14] | Sun and Abraham (2021) | 113 |
| [15] | Borusyak, Jaravel, and Spiess (2024) | 10 |
| [16] | Roth (2022) | 100 |
| [17] | Rambachan and Roth (2023) | 97 |
| [18] | de Chaisemartin and D'Haultfoeuille (2020) | 30 |
| [19] | Rosenbaum and Rubin (1983) | 99 |
| [20] | Stuart (2010) | 111 |
| [21] | Austin (2009) | 8 |
| [22] | Henderson, Storeygard, and Weil (2012) | 41 |
| [23] | McMillan and Rodrik (2011) | 76 |
| [24] | Landefeld, Seskin, and Fraumeni (2008) | 62 |
| [25] | North (1990) | 85 |
| [26] | Kurtz et al. (2000) | 60 |

## Full reference list (148 entries, author-sorted)

The list below contains all 148 sources in the assembled corpus, sorted by first-author surname and then by year. Each entry resolves to a digital object identifier (rendered as a clickable https://doi.org link) or, where no DOI exists, to a stable repository or archive URL. NASA Technical Reports Server items that the source feed indexed without a personal author byline are listed under the institutional author "Anonymous" with the NASA Technical Reports Server identifier preserved in the resolvable URL; their authorship can be confirmed at the linked record.

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## Appendix A. Variable and data dictionary

This appendix records, in one place, every construct the design measures, its operational definition, its source, its scale, and its known biases. It is the full form of the Chapter 4 measurement table, presented so that a reader can reconstruct each variable without recourse to the narrative. The dictionary is organized into four blocks: the treatment, the three outcomes, the matching covariates, and the auxiliary indicators used only in robustness and mechanism checks. The construct names are fixed by the shared bible and are not redefined here; this appendix only operationalizes them.

The treatment variable is the open-data-policy adoption event. Its operational definition is a binary indicator that switches from zero to one in the mission-period in which the mission's data transitioned to free-and-open release, and remains one thereafter, with the transition period taken from the hand-coded adoption register described in Appendix B. Its source is the register, which itself draws on mission documentation, Distributed Active Archive Center policy records, the NASA Plan for Increasing Access to the Results of Scientific Research, and the Science Mission Directorate Scientific Information Policy and its annual implementation metrics. Its scale is binary by period, with the adoption period g recorded as a cohort label so that the staggered timing is preserved for the Callaway and Sant'Anna group-time estimator [14]. Its principal known bias is the phased-transition problem: some missions did not adopt on a single clean date but moved through intermediate access regimes, so the binary coding introduces a date-assignment error that is handled by flagging phased transitions and testing sensitivity to alternative date definitions, never by smoothing the ambiguity away.

The first outcome is the publication rate, defined as the count, per mission-period, of peer-reviewed articles that use the mission's data, identified by the frozen bibliographic-linkage rule of Appendix C (mission and instrument name matching, dataset-identifier matching, and acknowledgment-text matching). Its source is the dual bibliographic frame of the NASA Astrophysics Data System [60] and Web of Science, cross-checked so the count does not depend on a single index's coverage frontier. Its scale is a non-negative integer count per period, which is why the estimating equation uses a count-appropriate Poisson or log-link form with explicit attention to the structural zeros common for small or young missions. Its known biases are the right-skew and over-dispersion of citation-linked counts, coverage growth in each index over the observation window, and linkage incompleteness when an article uses but does not name the mission in a parseable way; the frozen rule is the primary defense, and the no-prior-affiliation specification of Appendix C is the secondary one. A supplementary version of this same variable restricts the count to authors with no prior mission-team affiliation, operationalizing North's impersonal use [85].

The second outcome is the dataset-citation rate, defined as the count, per mission-period, of formal citations to the mission's datasets as first-class scholarly objects, following the Joint Declaration of Data Citation Principles [27] and the repository and publisher roadmaps that implement it [33, 40, 50]. Its source is the same dual bibliographic frame, restricted to formal reference-list data citations rather than informal in-text mentions. Its scale is a non-negative integer count per period, analyzed separately from the publication rate and restricted to the later window because formal data citation is sparse and biased downward early, a measurement reality documented for the field with the most public data [42]. Its known bias is therefore a time-varying undercount in the early periods, which is why the dictionary records this variable as available-late and why every report of it carries an explicit power caveat.

The third outcome is the distribution volume, defined as the count of access and download events recorded per mission-period by the Earthdata access infrastructure and the Distributed Active Archive Centers. Its source is NASA's Earth Observing System Data and Information System distribution record. Its scale is a non-negative count, used as a descriptive early-response outcome and as a mechanism check rather than as a precisely calibrated quantity. Its known biases are sensitivity to the definition of a download event, granularity changes in the delivered product, and inflation by automated and machine-to-machine retrieval that itself grows over the window; the dictionary records these so that the variable's direction and timing, not its level, carry the inferential weight.

The matching covariates are sensor class and mission age. Sensor class is a categorical variable with the fixed levels optical imager, synthetic aperture radar, lidar, passive microwave, and spectrometer, coded from mission instrument documentation. Mission age is the integer number of periods since the mission's operational start at each observation period. Both enter the propensity-score and matching machinery [99, 111] that constructs the comparison group within sensor-class-by-age strata, and both are recorded with their scales so the matching can be reproduced. Additional considered controls, recorded as auxiliary indicators, are the size of the relevant research community, the mission data-product maturity level, and the agency or international partner; these are listed in the dictionary as candidate controls whose inclusion is specified before estimation rather than chosen after seeing a result.


## Appendix B. Open-data-policy adoption register, schema and coding protocol

This appendix specifies the register that supplies the treatment variable, because the entire identification strategy rests on assigning each mission a correct adoption cohort. The register is a structured table with one row per mission and a fixed schema. The schema fields are the mission identifier; the prior access regime (restricted, fee-based, registration-gated, or already open at first observation); the open-data adoption date; the licensing status before and after the transition; the data-tooling status before and after, recorded against the FAIR vocabulary so that nominal openness is distinguished from functional openness [120, 80]; a phased-transition flag; and a source-citation field listing the documents that establish the date and regime. The schema is fixed before coding so that the register is a measurement instrument, not a narrative.

The coding protocol is double-entry with adjudication. Two coders independently populate the schema for each mission from the same source set, working blind to each other's entries. Disagreements on any field are logged and adjudicated against the primary source documents, and the adjudication rule is recorded so that a third party can replay it. The protocol's design purpose is to make the treatment assignment auditable: because the register is the single point at which a subjective judgment (when did this mission become open) enters an otherwise mechanical pipeline, the double-entry-and-adjudicate procedure is where the design spends its measurement discipline. Phased transitions receive special handling. A mission that moved through intermediate regimes is flagged, its candidate dates are all recorded, and the primary analysis uses the date of the first genuinely free-and-open release while a robustness specification re-runs the event study under alternative date definitions. This is the operational form of the prospectus commitment to test sensitivity to the adoption-date coding rather than to assert a clean date that the documentation does not support.


## Appendix C. Bibliographic-linkage rule and the no-prior-affiliation filter

This appendix specifies the rule that attributes a publication to a mission, because the publication and dataset-citation outcomes are only as credible as the rule that builds them. The linkage rule combines three matching channels. The first is mission and instrument name matching, in which an article is linked to a mission when its text or metadata names the mission or a named instrument carried by the mission, against a controlled vocabulary of mission and instrument names and their documented variants. The second is dataset-identifier matching, in which an article is linked when it cites a dataset whose persistent identifier resolves to a product of the mission. The third is acknowledgment-text matching, in which an article is linked when its acknowledgment or data-availability statement names the mission or its data source. An article matched on any channel is counted once; double counting across channels is prevented by deduplicating on the article identifier.

The single most important property of the rule is that it is frozen across the pre- and post-adoption periods. The same controlled vocabulary, the same matching channels, and the same deduplication are applied identically before and after a mission's adoption date. This is the operational discharge of the Kuznets within-versus-relabeling discipline [62, 76]: a rule that tightened or loosened over time would let a change in counting practice masquerade as a change in output, which is precisely the inference error the design exists to prevent. The no-prior-affiliation filter is a secondary specification layered on the publication outcome. It restricts the count to articles whose authors had no prior affiliation with the mission team, identified from authorship and affiliation metadata, so that the restricted count measures impersonal use by researchers who had to pay the access transaction cost the policy is alleged to lower [85]. The filter is recorded here as a fixed, pre-specified specification rather than a post-hoc robustness afterthought, so that agreement between the full and the impersonal-use counts is informative rather than a product of selection.


## Appendix D. Pre-registration record and result-table templates

This appendix records the pre-registration commitment and reproduces the specified-but-unpopulated result-table templates from the analysis plan, because the design's claim to credibility is that its parameters were fixed before estimation. The pre-registration record fixes, in advance, the outcome definitions of Appendix A, the matching covariates and procedure of Appendix C and Appendix A, the primary Callaway and Sant'Anna estimator [14] and the pre-specified robustness battery [113, 10, 30], the event-time window, the mission-level clustering with wild-cluster bootstrap inference, and the decision rule. The decision rule is reproduced verbatim from the shared bible: support for H1 requires flat leads, positive lags with a positive and statistically distinguishable overall effect, and survival of the Rambachan and Roth sensitivity analysis [97] at the stated breakdown threshold; failure on any of these falsifies the contribution, and positive trending pre-adoption leads void identification before the lags are examined.

The result-table templates are laid out with their column headers, their event-time rows, and the sensitivity-region structure specified, and their cells deliberately empty, consistent with the design-stage guardrail. The event-study table has one row per event-time period from the earliest lead to the latest lag, a column for the point estimate, a column for the confidence interval, and a normalization marker on the last pre-adoption period. The sensitivity-region template has a row per breakdown parameter value and a column recording whether the effect survives at that value. No cell in any template is populated, because no estimate has been computed on the full assembled panel. The templates are included so that the form of the eventual output, and the decision the output will trigger, are both fixed in writing before any number exists to tempt a post-hoc revision of the rule.


## Appendix E. Illustrative-simulation parameters

This appendix records the parameters of the illustrative simulation used in the analysis plan to demonstrate the shape of the event-study path and the operation of the decision rule on synthetic data. The simulation is explicitly a demonstration of the method, not a forecast of the result; every quantity in it is illustrative and is labeled as such, and none is an estimate of any real mission's effect. The simulation generates a synthetic panel of mission-periods with staggered adoption cohorts, draws count outcomes from an over-dispersed count process with structural zeros to mimic the right-skew and the small-or-young-mission zeros that the real outcomes exhibit, imposes a known data-generating effect with flat pre-adoption leads and a gradually building post-adoption path consistent with North's path-dependent adjustment, and then runs the full estimation pipeline on the synthetic panel to confirm that the estimator recovers the imposed path and that the decision rule fires correctly. The recorded parameters are the number of synthetic missions, the number of periods, the cohort structure and adoption schedule, the over-dispersion and zero-inflation parameters of the count process, and the magnitude and event-time profile of the imposed effect. These parameters are fixed in the pre-registration so that the simulation is reproducible and so that its only role, demonstrating that the pipeline behaves as specified before it is run on real data, cannot be confused with a result. The simulation thereby closes the back matter on the same principle that opened it: the design is offered as a reproducible specification, and reproducibility is itself an application of the open-data principle the dissertation sets out to test.