In this paper, I provide a guide for the conduct of empirical environmental social science (ESS), a type of social science that is closely related to the study of social-ecological systems and social-ecological research. It does so from a positivist perspective, emphasizing the collection of empirical data with the intent to uncover regularities across a set of observations. Castree et al. (2014:765) state that ESS “has two aims: (1) to study systematically the presuppositions, norms, perceptions, preferences, relations, regulations and institutions that together structure how humans value and use the non-human world; and (2) to identify and evaluate ways of altering human behaviour in light of one or more definitions of desirable or necessary ends. As part of this second aim, many environmental social scientists work with those effecting, or affected by, environmental change, rather than just conducting research on them.”
ESS is a highly interdisciplinary and frequently participatory area of research that incorporates many scientific approaches, including institutional analysis, ecology, political ecology, geography, and anthropology, as well as the study of complex social-ecological systems. ESS is thus a highly diverse and interdisciplinary approach to science. This diversity and the exploratory nature of many ESS analyses, although providing important benefits to the communities of researchers involved, has left several gaps in the literature. One primary gap is that there are few standard instructional materials for this area of research. Several edited volumes and articles that synthesize ESS-based approaches do exist (Young et al. 2006, Moran 2010, Vacarro et al. 2010, Manfred et al. 2014), and the foundational literature on social science methods is substantial (e.g., see King et al. 1994, George and Bennett 2005, Bernard 2011). However, to-date there has been little integration between these two literatures to provide a synthetic rubric for the conduct of ESS. My aim is to fill this instructional gap by providing a research rubric that is tightly integrated with the ESS literature. Methodological concepts are presented with explicit reference to examples from ESS and are accompanied by discussions of the prevalence and importance of each concept within the ESS literature. Concepts and issues that are highly prevalent in the ESS literature are emphasized throughout.
I do not claim to provide an exhaustive treatment of ESS or of the different methods and methodologies that it encompasses. What this paper integrates is a particular subset of ESS with a particular set of methodological literature. It does not synthesize all ESS-related literature. Specifically, I do not cover quantitative social-ecological modeling and scenario-building techniques, which have been enormously important parts of the ESS literature, but have each received much attention elsewhere. My primary goal is to enable the beginning environmental social scientist to plan a research project and write a proposal that would guide such a project.
To support the text in the main body of this paper I have included several appendices. Key terms are defined in Appendix 1. For a more basic review of scientific terminology, e.g., concepts, variables, or theories, that is used throughout the paper and throughout ESS, the reader should refer to Appendix 2.
There are four primary elements of a research project that need to be developed and carried out to address a research question. These include (1) the research design, (2) the sampling methodology used to target observations, (3) measurement protocols used to collect data on the chosen observations, and (4) the analytical techniques applied to the collected data. For interested readers, Appendix 3 describes another important element, this being the extent to which the research project is primarily inductive vs. deductive. Additionally, Appendix 4 summarizes a real ESS research project in accordance with the terminology developed here to demonstrate how these concepts can be used to descriptively summarize any given project.
A research design is just that, a design that a research project employs to address its research questions. A taxonomy of research designs, or study types, is presented in the following list:
The most common distinction among research designs is based on the extent to which they incorporate an experimental element (Bernard 2011). Essentially, an experiment is defined by its ability to isolate the effects of one or very few factors by controlling the variation of other variables across what are termed “control” and “treatment” groups. By randomly assigning observations to one of these two groups and then applying the treatment to the treatment group, the experimentalist minimizes the systematic difference between this group and the control group, other than the presence of the treatment, which can then be the only systematic explanation for differences in outcomes observed across the two groups. This increases their internal validity (to be discussed later) by limiting the possibility that alternative explanations could threaten causal inferences made in the subsequent analysis.
Within many scientific circles, there is a lot of rhetoric about the importance of experiments as the only fully valid way of establishing the importance of an independent variable. However, it is important to observe that their source of scientific strength is also the source of their primary weakness (Kauffman 2012). Experiments are comparatively poor at representing causal complexity and interaction effects. They are also usually conducted over relatively short time frames. As a result, they have comparatively low ecological validity, which, as I will discuss later, represents the extent to which we can generalize their results to real-world settings.
Experimentalists can incorporate additional complexity by conducting a factorial experiment, which essentially introduces additional independent variables, or treatments, into the design to examine interaction effects between these variables and the primary treatment variable. This quickly increases the number of distinct subgroups involved. For example, instead of having one control and one treatment group, an experiment with two independent factors as treatments would need to include one group for every possible combination (presence, absence) of each treatment, or four groups. Such designs can quickly become expensive and onerous, and it is unlikely that it will ever be feasible for them to mimic the complexity of real-world environments.
Recently, the field of development economics, which overlaps with ESS, has taken a distinctly experimental turn, most boldly embodied by the efforts of the researchers at the MIT Poverty Action Lab (http://www.povertyactionlab.org/). A primary outcome in this research has been the adoption of new agricultural technologies and knowledge, while common treatments include various financial devices and services. The field of ecology has also become highly experimental at small scales in the past several decades (Sagarin and Pauchard 2012).
The majority of analyses in ESS are nonexperimental. Those that are experimental tend to occur in the lab or in small field settings because large-scale experiments are usually untenable on account of resource limitations and the simple political infeasibility of the social changes that would be required. Such experimental ESS research is largely focused on the determinants of human behavior and cooperation because these affect environmental conditions (Ostrom 2006, Cox et al. 2009).
When true experiments are not feasible, researchers may turn to quasi-experiments, which are essentially experiments in which the assignment of observations to a treatment or control group is nonrandom. If neither true nor quasi-experiments are feasible, then the research can turn to an observational study. In such studies, “researchers do not attempt to change or manipulate variables to test their effects; they simply observe or measure things as they are in the ‘natural,’ unaltered world” (Remler and Ryzin 2011:355). Natural experiments are a cross of being experimental and observational studies. A natural experiment takes advantage of some naturally occurring treatment that is “applied” to one group, but not to another, highly similar, group. Such naturally occurring treatments can be environmental policies, or natural events such as floods and forest fires.
The final two observational categories (correlational study and case study) represent the great majority of data-oriented analysis in ESS. A correlational study involves a large enough number of observations to warrant a statistical or qualitative comparative analysis of many observations. Correlational studies are important in ESS for their ability to facilitate cross-observation generalizations, although for the most part their units of analysis are small, e.g., households, so generalizability across larger contexts is often still limited (Poteete et al. 2010). There are exceptions to this (see Gutiérrez et al. 2011).
In contrast, a case study (1) examines only one or few “cases” or observations of its primary unit of analysis, (2) involves multiple units of observation/data sources that it uses to draw inferences about each case, and (3) generally involves the measurement of more variables than observations, a situation that precludes statistical analysis in favor of qualitative analysis. ESS has traditionally involved many case studies (Lansing 1991, Ernst et al. 2013, Gilbert 2013, Kitamura and Clapp 2013). ESS case studies are generally distinctive for having some sort of social-ecological system as their unit of analysis, or the case that they examine.
When qualitative and quantitative approaches are combined the result is frequently referred to as a mixed methods approach. More specifically, a correlational analysis combined with a case study creates an embedded case study analysis (Yin 2014). The way in which these two research designs can be connected is based on the nested nature of reality: many entities exist in one-to-many relationships with each other because of the hierarchical nesting of social and biological life. Individuals lives within communities, which may exist within larger social units, and so on. Therefore an embedded case study may involve a qualitative analysis at the level of the case, but a researcher may collect data on enough observations of a nested unit of analysis to warrant a statistical analysis at this more disaggregated level. Ideally such analyses are complementary. For example, a researcher may compare four forests, but may do so by collecting tree-level data upon which he/she conducts a statistical analysis. If the researcher collects enough data at both levels (enough forests and trees in this case) he or she could conduct a multilevel statistical analysis at both levels of organization. Embedded case studies are very common in ESS, with projects that target a particular social-ecological system examining this system by collecting data and conducting analyses of units embedded within this system (Acheson 1975, Vogt et al. 2006, Ayers and Kittinger 2014, Snorek et al. 2014).
Finally, there are synthetic studies that rely on aggregating secondary data and information from existing analyses, rather than collecting their own primary data. Primary data have yet to be collected by anyone, and need to be collected by the researcher. Secondary data are already present, at least in some form, although they may need to be reorganized, e.g., via some content analysis, in some way before the researcher can analyze them.
The most informal type of synthetic research design is simply a qualitative literature review that seeks to summarize the findings of a set of previous projects. A literature review is in fact frequently part of a larger project, but also can stand alone as a more hypothesis-driven type of research exercise (see Biggs et al. 2012). When it is systematized to enable a formal analysis of its own, it is referred more often as a case study meta-analysis or systematic review. In some fields the term meta-analysis refers specifically to the aggregation of multiple statistical studies, either by directly pooling quantitative data, or by pooling the results of multiple statistical analyses, e.g., pooling effect sizes. In ESS, it has tended more to mean the extraction of quantitative data from primarily qualitative case studies via a content analysis coding process (Rudel 2008). Such analyses generally either analyze the cases described in published studies (Cox et al. 2010, Evans et al. 2011, Cox 2014a) or use the studies themselves as their unit of analysis (Geist and Lambin 2002).
Systematic reviews initially became popular in public health-related fields (http://www.cochrane.org/), but have more recently spread to ESS-related disciplines (http://www.environmentalevidence.org/; Pullin and Stewart 2006, Bilotta et al. 2014). A systematic review involves the analysis of secondary data to explore the effects of a particular intervention, via either a qualitative narrative analysis or a statistical meta-analysis that combines quantitative data from the synthesized studies to calculate aggregate effect estimates of the intervention in question.
A sampling strategy is generally the process of selecting a sample to study from a population of observations, say, trees in a forest. We collect a sample because we usually do not have the time or resources to collect data on an entire population of interest. The number of observations in a sample is referred to as the sample size. If we do collect an exhaustive sample of the entire population, this is called a census. Otherwise we want a representative nonexhaustive sample, or a sample with attributes that reflect the overall characteristics of the larger population. If we collect a biased sample for some reason, referred to as sampling bias, this means that we have somehow systematically identified or selected for one type of observation to sample over other types within the population. A biased sample is not representative of the larger population.
There are several dimensions that can be used to distinguish different types of sampling strategies and the sample types that result. First, a sample can be (1) random or nonrandom, and (2) stratified or nonstratified. Stratified samples can in turn by proportional or nonproportional. These distinctions create the basic typology of sample types as shown in Table 1. A random sample is just that, random. These are seen as a gold standard of sorts because they are the best way to ensure that a sample is representative of the larger population.
In practice, however, we frequently do not pursue a random sample for the following reasons: (1) because of the lack of a sampling frame, or a well-defined list of accessible observations, (2) the inability to collect data from randomly selected observations, (3) we are conducting a case study analysis of a small number of observations, and (4) we in fact do not want a representative sample. This final case occurs frequently when we are conducting key informant interviews, in which we target a select group of individuals and ask them about the system of which they are a part.
A sample can be stratified to account for large amounts of heterogeneity within the target population. This divides the population into strata along a dimension of particular theoretical importance, such as a demographic characteristic for a social study, or a biophysical gradient in an ecological one, and then collects a sample within each of these categories. Stratified samples can be stratified proportionally or nonproportionally. A proportional sample is one in which the numbers of observations within each strata are collected to be proportional to their presence in the larger population.
Purposive samples are nonrandom and nonstratified. These are guided by the researcher’s judgment regarding what are the most appropriate observations to analyze with a sample. Common criteria for such judgments include (1) the expertise held by certain human respondents, in which case the sampling method is known as expert sampling, (2) the representativeness of the observations of the population, or conversely (3) the deviance of a particular case or observation from the population, if this deviance is to be explained.
Two types of samples that can be considered as subsets of purposive samples are (1) snowball samples and (2) convenience samples. A snowball sample is produced by a nonrandom sampling procedure in which initial observations are used to identify and access subsequent observations. This procedure is specific to human subject observations, who have the ability to identify other potential interview respondents. Given the importance of social networks, trust, and reputation in human interactions, this method is frequently the most, or only, feasible way to obtain access to many remote respondents. A convenience sample is produced when the researcher selects observations almost entirely based on their availability, or the convenience of obtaining data from them.
Finally, a multistage sample is one in which an initial set of observations are selected, and then for these observations, multiple measurements are taken to ultimately produce many new observations per each original observation. This can happen in two basic ways: the original observations are selected, and then measurements are made for each observation at multiple periods in time to create what is known as panel data. Panel data enable both cross-sectional and longitudinal comparisons. The other way occurs when clusters of observations are first selected, and then a second sampling technique is applied to observations nested within these clusters. This is known as cluster sampling. A cluster could be a school, city, or forest, or parts of a forest, in which case each cluster is spatially explicit, and the nested units (say trees) would be physically nested within the cluster. In ecology this method is known as transect sampling, the clusters being called transects, and it is generally used to estimate the abundance and distribution of different species in an area. Cluster sampling and stratified sampling are similar, each involving an initial breakdown of the population based on some criterion. One main difference is that generally all strata are examined, while this is hardly ever the case for clusters.
Measurement occurs in two steps (see Adcock and Collier 2001 for a more expansive discussion). These are depicted in Figure 1. In the first step, a concept is operationalized into a variable and assigned a particular range. In the second step, this variable is measured via a data collection method and/or instrument. One necessary part of operationalization is deciding on the level of measurement for a variable. The following presents a very common scale that is used to classify different levels of measurement. Note that I include qualitative as a category here.
It is also important to note that there need not be a one-to-one relationship between a concept and a variable. In fact, it can be useful to have multiple variables for a given concept to ensure that the results of an analysis are not idiosyncratic to a particular type of operationalization. The process of checking one way of measuring a concept against others is referred to as triangulation (Yin 2014). ESS frequently involves both nonhuman observations and human observations, or respondents, which produce objective data vs. subjective data, each of which can be used to check the validity of the other. In the study of forest management, for example, both objective and subjective data have been commonly used to measure the concept of forest health. Nagendra and Ostrom (2011) show that in some cases these give comparable evaluations of forest condition.
Once concepts have been operationalized and observations sampled, the researcher needs to decide what measurement strategy he or she will employ to make measurements on the selected observations. The first set of such options involves soliciting responses from human subjects regarding written or spoken questions (see Fowler 2009 for a discussion of surveying techniques). Informal interviews are in fact not interviews the way most people think of the term, but are essentially informal conversations that a researcher has with human subjects during the course of, say, a fieldwork season. Unstructured interviews are also rather informal, but actually occur as interviews, and are understood as such by both the subject and the researcher. Focus groups are a bit like unstructured interviews but occur in group settings, with multiple respondents at once. Semistructured interviews involve the use of an interview guide to make sure that certain subjects are covered and certain questions are asked. Finally, structured interviews are done with the help of a written questionnaire that the researcher fills out as the subject responds to the questions it contains. Self-administered surveys are like questionnaires, but are filled out by the subjects without the presence of the researcher. As this list indicates, there is a range of formality a researcher might impose in the data collection process, and in the research design in general, and the researcher faces a trade-off between the goal of obtaining data that have a high probability of being consistent across observations and thus answering the original research questions if analyzed appropriately, and the goal of adapting to changing circumstances as the project proceeds.
Next, Participant observation involves researchers becoming actively involved in a particular system to the extent that they gain knowledge of everyday and subtle causal complexities of that particular system which are hard to otherwise capture and can be difficult to generalize. It usually involves fieldwork in the study site and extensive note-taking. It has been most commonly practiced by anthropologists (see Bernard 2011), although Sagarin and Pauchard (2012) argue that a similar approach is critically important for the discipline of ecology, to complement more experimentally manipulative approaches.
Similarly, but with less direct involvement and engagement, direct observation can be conducted with any type of subject, and it involves the researcher directly observing the behavior of the subject, which is usually a live organism, if not a human. In comparison with participant observation this is generally seen as a more quantitative approach, with the aim frequently being to count frequencies of certain behaviors or otherwise make quantitative measurements based on what is being observed during a particular period of time (Guest et al. 2012).
Direct observation can be aided by technology, in which case the researcher is also using in-person instrumentation, which is the use of a technological device to record data about an environment, or to take samples from this environment. This technology could be a recorder or a video camera, or in the case of biophysical scientists it could be any range of data collection instruments. Finally, remote instrumentation likewise involves the use of some technology to collect the data, but does not involve or require the presence of the researcher.
Analysis is the process of describing and then making inferences based on a set of data. To make an inference means to combine data with something else, say a set of assumptions or theories or more general knowledge, and draw a conclusion that goes beyond what the data themselves present. The most basic distinction we can make between different types of analysis is to classify them as either quantitative or qualitative. A quantitative analysis is mostly associated with correlational studies, and it involves the examination of relationships between quantitative (categorical, ordinal, and interval/ratio) variables, whereas a qualitative analysis does not deal with numerical data. A qualitative analysis is generally done as part of a case study, and instead involves the construction of inferences from nonnumerical data sources.
It is possible to transform qualitative data into quantitative data via what is known as content analysis, which has been done by a fair number of ESS scholars (Delgado et al. 2009). There are many textbooks (Neuendorf 2002) and software packages available for this (Atlas.ti and NVivo). Importantly, the qualitative medium need not be in the form of text as a text variable, but can be any medium, such as videos or direct in-person observations. In addition to content analysis, quantitative data can be used to produce other quantitative data, in two basic ways: (1) transforming a variable at a “higher” level of measurement to a “lower” level of measurement, e.g., from an interval to an ordinal variable, and (2) calculating averages to summarize sets of observations and produce a new, more succinct, dataset.
Statistical analysis is the primary analytical tool in many scientific fields, and it is probably the most commonly used quantitatively analytical tool in ESS and related disciplines (Agrawal and Yadama 1997, Hayes 2006, Lorent et al. 2009, Persha and Blomley 2009, K.C. 2013). Grounded in probability theory, statistical analysis primarily involves the application of calculations to a dataset to (1) describe a sample, (2) make statistical inferences about a population by constructing confidence intervals and conducting hypotheses tests, and (3) estimate the magnitude of associations between variables. Much of this is done via statistical modeling. There are numerous textbooks and online resources for introductory to advanced statistics. The most popular statistical software packages include SPSS, SAS, JMP, Stata, and R.
Network analysis, most commonly conducted by ESS researchers as social network analysis (SNA; Cohen et al. 2012), involves the conceptualization of a network of nodes connected by a series of links (see Borgatti et al. 2009 for a summary of the practice of SNA). In ESS, the nodes are most commonly social actors, such as resource users or managers, but this is not necessarily the case. The links connecting different nodes are generally identified based on their theoretical importance. Examples of links “include routine interactions among actors regarding environmental policy issues (Schneider et al. 2003), exchanges of information regarding a natural resource, fishing gear exchanges, and social support activities (Bodin and Crona 2008), and exchanging ideas and funds (Lauber et al. 2008)” (Cox 2014b:312). There are numerous social network software applications (e.g., Ucinet), and R actually includes several network analysis packages.
Within ESS, social network analysis is one of the fastest growing types of analysis (Prell and Bodin 2011, Isaac et al. 2014). However, a primary limitation of network analysis in ESS is the resource-intensity of the data collection required. This is because network analysis typically requires one to collect data from every node in a network, which is not cheap or easy, particularly if the nodes live in a remote community that is not very small.
Geographic information systems (GIS) and remote sensing (RS) refer to suites of hardware, software, and analytical techniques designed to collect and analyze spatial environmental data, that is, data describing observations with spatial coordinates. In fieldwork-based ESS these are frequently complemented by Global Position System (GPS) units to collect local spatial data (see Brondizio and Roy Chowdhury (2010) for a summary of the application of these technologies and techniques in ESS).
GIS operations are applied primarily to vector-based data, or data expressed as discrete points, lines, and polygons. The most popular GIS software package is ArcGIS. The term remote sensing most accurately refers to the remote detection of radiation that is reflected or emitted by different objects or land surfaces. This process produces images made up of cells, or pixels. RS operations are then applied to raster-based data, or images, primarily in the form of satellite imagery, e.g., via the Landsat program, and aerial photography. RS technologies and operations are used extensively by scholars studying land use and land cover change (Lambin et al. 2001, Vogt et al. 2006). Many environments and natural resources that cannot be easily monitored otherwise can frequently be feasibly measured with the aid of remote sensing technologies (Andersson et al. 2008). Given the explosion in availability of spatial data, these tools are likely to only increase in importance in ESS. Several common RS applications include ERDAS IMAGINE, ENVI, and IDRISI.
Qualitative comparative analysis (QCA) is an approach that is designed to compare quantitative data on a medium to small number of observations without the normal emphasis on effect sizes and formal hypothesis testing that dominates the statistical approach. It places more of an emphasis on interaction effects and conditions of causal necessity and sufficiency than the normal statistical approach does. It has been championed primarily by Charles Ragin (1987, 2000).
QCA is essentially built on the notions of necessity and sufficiency combined with the causal logic established by John Stuart Mill. Without diving too much into the details, which can easily be found online, this logic enables us to examine Table 2 and conclude that, of the four aquaculture farms shown there, the outcome can be explained by the use of tilapia is the primary fish. This is because (1) it is the only potential cause that is present in all successful cases, meaning that no other cause is necessary, and it is sufficient, and (2) it is the only cause that is absent in all unsuccessful cases, meaning that no other cause is sufficient, and it is necessary. It is important to note that although supposedly not as rigorous as statistical analyses due to the small number of observations involved, the intuition here is used effectively by humans in all walks of life. Ragin’s QCA method essentially elaborates on the logic proposed by Mill, and has been by several researchers studying social-ecological relationships (Rudel 2008, Basurto 2013, Pahl-Wostl and Knieper 2014).
Each of the previously mentioned analytical strategies relies on analyzing quantitative data, which are data that are produced ultimately by breaking a continuous world up into discrete chunks and counting and measuring features of these chunks so that they can be compared. Whenever this is done, some information and complexity is inevitably obscured or lost. Ideally, that gap is where purely qualitative analysis steps in.
There are several types of qualitative analysis that ESS scholars frequently conduct. These include (1) thick description, (2) narrative path analysis, (3) qualitative models that depict relationships of the sort shown in Figure 2, (4) congruence testing, and (5) inductive theorizing. Although I describe them as types of qualitative analysis, each is frequently integrated with quantitative data analysis and numerical methods (and vice versa). Each of these methods is also used frequently with the others.
Thick description was popularized as an analytical strategy by Clifford Geertz (1973), who played a prominent role in the development of qualitative ESS (Geertz 1959, 1980). Thick description is characterized, and contrasted with thin description, by Denzin (1989:33) by having the following functions: “(1) It gives the context of an act; (2) it states the intentions and meanings that organize the action; (3) it traces the evolution and development of the act; (4) it presents the action as a text that can then be interpreted. A thin description simply reports facts, independent of intentions or the circumstances that surround an action.” Some form of thick description is frequently a central part of an ESS case study.
Often what ESS scholars describe about a case is the historical development of the case’s ecological or social components, and the relationships between these. The scientific field that uses this approach extensively has frequently been referred to as environmental history (Diamond 1997, 2005, Cronon 2011). Such studies exemplify the standard features of a case study, particularly in that they tend to rely on many sources of evidence to support the theories they promote.
Many concepts such as “path dependence” that are prevalent in ESS are explicitly temporal and historical. This is reflected in the emphasis that many case studies place on unpacking historical dynamics and, in turn, extrapolating from these to explore future scenarios for the paths that a system might take in the future. These narrative path analyses frequently break out the history of a system into discrete chunks of time, and rely on a scientific framework to theoretically inform the characterization of these time periods and the relationships between them (Brown et al. 2013, Boonstra and de Boer 2014, Câmpeanu and Fazey 2014, Cody et al. 2015). In such analyses, the cumulative impacts of historical events and the resulting path-dependency of the current situation are often emphasized. In case study methods textbooks (see George and Bennett 2005), this has been referred to as process-tracing, and several ESS scholars have begun to implement this as an analytical strategy (Fleischman 2014).
More formally, a scientist can explore the structure of a system with a qualitative model. These go by many names, including access mapping of commodity chains (Ribot 1998), influence or logic models, arrow diagrams (Homer-Dixon 2010), path diagrams (Fleischman 2014), impact or linkage diagrams, and causal loop diagrams (Sendzimir et al. 2011). Qualitative models are generally represented as “box-and-arrow” diagrams, and the common denominator of each such model is that it breaks a system or process down into a set of constituent objects (boxes) and the directed relationships among these objects (arrows). Such models are in fact ubiquitous in the ESS literature as a way of developing an understanding of the system in question, particularly in case study analyses (Neudoerffer et al. 2005, Homer-Dixon 2010, Alberti et al. 2011, Österblom and Sumaila 2011, Fazey et al. 2011, Downing et al. 2014). The objects can take a variety of forms, and increasingly these objects are closely tied to elements of social-ecological systems identified in supporting social-ecological frameworks (see Villamayor-Tomas et al. 2014 and the associated special issue). The presentation of a qualitative model is most often accompanied by a narrative that describes the components and how they represent important dynamics within the target system or process. Such models are frequently developed collaboratively with local resource users and other participants to explore scenarios for future change in the target system (Marín et al. 2008, Delgado et al. 2009, Guimarães et al. 2013).
Qualitative work can also be explicitly comparative. Some scholars have qualitatively compared small numbers of cases informally, through simple nonquantitative comparisons that do not attempt to formally characterize the relationships among the variables. These may be done by making comparisons of the sort shown in Table 2, although not necessarily with the intent to establish necessity or sufficiency (Klooster 2000). Longitudinally and cross-sectionally comparative case studies in ESS are also frequently done by applying a formal scientific framework to different cases or to different time periods within one case (Pahl-Wostl et al. 2013, Barnett and Anderies 2014).
Some ESS case studies compare the findings of a case with one or more theories that describe expected findings in the form of a configuration of values for a set of variables (Fleischman 2014, Fleischman et al. 2014). This has been referred to as congruence testing (George and Bennett 2005) or “pattern matching” (Yin 2014). This is a method that examines the extent to which the main features of a case study are congruent with the hypotheses generated for this case by a theory. For some it has been standard wisdom that single cases cannot do much to confirm a theory (but may do much to contradict from a Popperian perspective). The extent to which a theory can be supported by a single case study depends in large part on whether or not the results of the case study can be explained by alternative theories or not. If the properties of a case are highly congruent with the expectations generated for it by a certain theory, and there are no alternative theories with which the case is also congruent, we may conclude that the results of the case are very unlikely except if they are explained by the theory, and this can be seen as strong evidence in support of the theory. As George and Bennett (2005:117) put it: “an explanation of a case is more convincing if it is more unique, or if the outcome it predicts could not have been expected from the best rival theory available.” This is made possible by having well-established theories with many independent predictions for a case. The more predictions, the more points of congruence can potentially be established and the less likely it is that a confirmatory case could be explained without the theory in question. “This process relies on Bayesian logic-the more unique and unexpected the new evidence, the greater its corroborative power” (George and Bennett 2005:219).
Finally, the inverse of the deductive process of theory testing (see Appendix 2) is inductive theory-building, or simply theorizing. This is the essentially qualitative process of inferring generalized, usually causal, relationships from a set of data, be it quantitative or qualitative. In addition to being an important part of quantitative studies, this is frequently done through single and comparative case studies, with a general pattern being that an author introduces a theory, and then presents one or more cases that exemplify this theory (Holling and Meffe 1996, Scott 1998, Robbins 2000). A standard observation here is that the same data used to develop a theory inductively cannot be used to then test that theory through some congruence procedure as just discussed.
A research project needs to be of some interest or importance to a definable audience. Frequently this audience is a community of scientists that works on the same family of research questions with broadly similar methods. One of the most common ways for a research project to be of interest to such a community is for it to identify a particular gap in the knowledge that has been established by that community. Other communities can be considered as well, such as environmental practitioners or a client that has contracted with a researcher to conduct a project, such as the United States Agency for International Development.
Feasibility is simply the extent to which a research project can be effectively conducted given the resources available to the researcher(s) considering the project. These resources can include time, money, equipment, and human capital and skills. These resources can of course be developed and obtained for the purposes of a particular research project, but unrealistic assumptions regarding the ability to do this, particularly in a short amount of time, should be avoided.
The relationship between research and ethical considerations has a very long and sometimes checkered history. I will not delve very much into these issues here, except to say that any researcher should of course consider whether or not the research they propose would unduly harm, or place at risk, vulnerable or disempowered populations.
Internal validity is the extent to which a causal inference made by an author correctly reflects a causal relationship between two or more variables. Two perspectives have predominated in discussions on the best method for understanding a causal relationship: one is the experimental/comparative perspective, and the other is the mechanistic/noncomparative perspective. The former views causation as being primarily detectible through ideally experimentally controlled comparisons, and secondarily through less controlled comparisons. Without comparing one observation with others, so the thinking goes, we have little leverage to gauge whether changing one variable will affect the value of others. This problem is often expressed in terms of counterfactuals. A counterfactual is an alternative scenario to which a realized scenario is compared to evaluate the significance of a causal factor that changes across the scenarios. Our interpretation of the causal significance of any factor depends critically on the most likely counterfactual to which the realized scenario is compared. In climate change and forest-related policies, this is expressed as the need to establish the additionality of a policy (Angelsen 2008). Additionality, most broadly, is the difference between the value of an outcome after the implementation of a policy and its value in a counterfactual scenario in which the policy is not enacted.
Establishing a counterfactual depends on finding observations that represent a primary scenario and others that reflect an alternative scenario, which, in a nonexperimental observational study, we can only do by making cross-sectional or longitudinal comparisons. For example, we might ask what the effects of a reforestation policy are on forest cover, and to do so longitudinally we would need to take into account the rates of reforestation or deforestation occurring prior to the implementation of the policy (this is referred to as establishing a baseline). The effect of the policy would be the difference between this rate and the rate sometime after the policy was implemented. To conclude, from the comparative perspective, we want to ask the following questions as ways to establish causal inferences:
From the noncomparative perspective, our primary concern is less about establishing counterfactuals, and more about whether or not we have a theoretical/mechanistic account that explains how or why such a covariation would occur. This perspective follows the aphorism that “correlation doesn't equal causation,” and argues that we cannot infer causality without a notion of mechanism, or theory that explains how one factor actually affects another.
In addition to identifying sources of effective causal inference, the literature on social science research methods has established possible threats to such inferences. There are two main types of such threats. The first is that an alternative narrative or story could explain the patterns, or covariations, we find in the data. The second source is that the data might not tell the whole story, and that the effects of an independent variable (IV) on a dependent variable (DV) are not fully accounted for.
First, there are two main ways in which a covariation between two variables might not support an inference that one causes the other. The first such alternative explanation is something we have discussed before: endogeneity or the possibility to that the supposed DV in fact causes an IV to change, rather than, or in addition to, the other way round. The data themselves may not tell us which direction the causal arrow points between two variables.
The second such threat involves sources of spurious relationships, in which an association between two variables is not actually indicative of a causal relationship, or at least the strength of this relationship. Inferring an effect where there is none is an example of committing a type 1 error. A type 2 error would involve the opposite: inferring the lack of a relationship where there really is a relationship. The primary source of a spurious relationship is a confounding variable. Confounding occurs when an independent factor, A, is found to correlate with a dependent factor B, when in actuality both are caused by a third phenomenon, the confounding variable C. This is shown at the bottom of Figure 2. For example, we might find that communities that use private property rights to manage a resource are more productive than those that use common property. However, if in fact common property is an adaptation to high environmental and economic scarcity (Barbanell 2001), then it could be that a third variable, resource scarcity, explains the presence of both in some systems, and in so doing explains the association between property rights systems and productivity.
The final threats are all ways in which an intervention could affect areas outside of its target area, and thereby complicate causal inference (see also Lambin and Meyfroidt 2011). First, we have diffusion of treatments or spillover effects. The idea here is that these effects need to be taken into account to accurately summarize the effects of the intervention. Each of these terms reflects either a positive externality, in which the effects of the intervention on untreated units is positive, or a negative externality, in which the effects are negative.
Regarding positive effects, in the study of marine protected areas, it is often hypothesized that the benefits for biota within the protected areas might spill over, or positively benefit, surrounding areas (McClanahan and Mangi 2000). Another term used to describe this phenomenon is diffusion (“diffusion of treatment” or “technological diffusion”). This has most often been used to describe the potential for the effects of a technology to spread or otherwise benefit subjects other than those provided the technology. Historically this has been most commonly applied to the potential spread of agricultural technologies (Hayami 1974). For example, if we were to provide a group of farmers in Kenya with cell phones that they could use to obtain weather information, it is possible that their neighbors could also benefit from this by talking with them. Comparing a treatment and control group in this context could lead to us undervalue the benefits of the phones. From a policy perspective, it is probably desirable to encourage these positive externalities. However, if unaccounted for analytically, they may cause a researcher to undervalue the positive effects of a policy.
Of course, new technologies and governance arrangements can have negative external effects as well. These could be simply negative externalities, such as when providing farmers with new pesticide technologies creates costs for other farmers who have not been provided them (Wilson and Tisdell 2001). Aside from this, the term leakage has become popular as a way of referring to situations in which the behavior or outcome that is forbidden in one area subsequently leaks out to other areas. Leakage has been widely discussed as a possible result of policies designed to mitigate climate change by preventing deforestation (Fahey et al. 2010). By preventing deforestation in one area, such policies might heighten incentives to cut down trees in other areas.
Finally, we have what Lambin and Meyfroidt (2011) refer to as a cascade effect, or an indirect effect that an intervention has on an outcome in areas other than that for which the intervention was intended. These are similar to spillover effects but are less direct. As a prominent example, the development of biofuels in developed countries has tended to incentivize agricultural expansion in developing countries via increased crop prices, thereby potentially negating much of the positive effects that increased biofuel production might have for climate change mitigation (Lapola et al. 2010).
External validity is the ability to generalize the findings of a study to other contexts, and could also be called inductive validity. There are two types I discuss: (1) generalizability from a sample to a population, and (2) generalizability from a population to other populations.
Each of these involves generalization from one set of observations to a larger set. The first of these has been the most frequently discussed in methods texts, and is the motivation behind the common desire to obtain a representative sample in moderate to large-n research projects. The intuition is that if we want to tell a scientific story about a population, and we can only really examine our sample, then we want to be able to generalize our findings about our sample to the population of interest.
The second type of external validity concerns whether or not the findings from a study can in fact be generalized to populations other than the primary population of interest. A study might take a sample of 300 Kenyan farmers out of several thousand farmers in a particular area, and if this is done randomly, or purposively in a way to achieve representativeness, then the findings of the study may be generalizable to the larger population of several thousand. However, we would still face the question of whether or not such findings would be generalizable to all Kenyan farmers, or all farmers in East Africa. Another example comes from work on toxicology, in which experiments on rats are frequently conducted to examine whether different substances are overly toxic. One possible criticism of this approach is the potential lack of generalizability from the population studied in these experiments to the population that we presumably care more about (humans).
The next two types of validity deal with a combination of causal inference (internal validity) and generalization (external validity). Each results at least in part from interaction effects that complicate causal inference. The first of these types is what I will call deductive validity. Rather than applying findings of a sample to a larger population or to other populations, deduction involves the application of findings regarding a sample to a smaller sample, or subgroup, of that sample. This process, rather than being inductive, is better described as a process of deduction, or applying general findings to a specific case.
Interaction effects are the primary threat to deductive validity. Referring back to Figure 2, if the IV is an intervention and the moderating variable is a distinguishing feature of two sets of cases in our sample, say, low development and high development countries, then we do not necessarily want to apply the same intervention to both areas of high and low development. Assuming that the policy would be effective in low-developed areas based on a sample-level positive effect could be deductively invalid, and doing so is sometimes referred to as committing the ecological fallacy.
Ecological validity is the extent to which the findings of a research project are generalizable to relatively uncontrolled contexts or environments. In ESS, generalizability to real-life contexts is invaluable, given the potential applicability of the work to the resolution of socio-environmental problems. A lack of ecological validity is of particular concern for experimental work, because experiments are defined as much as anything by the high degree of control that is exerted to isolate the effects of one particular factor on an outcome of interest. Because of this control, the findings from an experiment may not hold in a natural environment. For example, experiments are very popular in agricultural research, where highly similar plots of land are separated into control and treatments groups, and a treatment is applied to one group but not the other. This is done to accomplish the experimental goal of isolating the importance of one particular factor by ensuring that no other potential independent factors vary across the control and treatment groups.
This type of experimental control can come at the expense of being able to generalize these findings to much less controlled environments, where many variables may interact with those included in the experiment. Low generalizability also can result from the limited time-frame of an experiment. In such situations it can be difficult to establish permanence, or the extent to which relationships that hold over the short-run also hold in the long run after the initial intervention has run its course. For example, Hanna et al. (2012) find that when implemented in real-world settings over a substantial period of time, the benefits of improved cooking stoves in developing countries are not nearly as high as they are predicted to be by laboratory studies.
Measurement validity refers to the accuracy of each of the steps depicted in Figure 1 (operationalization and measurement). The protocol by which a concept is operationalized as a variable determines how faithfully the resulting variable reflects what is meant by the theoretically important concept. In the second step, error may come from (1) the data collection instrument itself, whether it is a written questionnaire or a physical device that records environmental data, or (2) the use of the instrument.
The measurement of concepts in ESS is tricky given the nature of the concepts used. Young et al. (2006) comment on this issue, particularly with respect to dependent variables such as sustainability and adaptive capacity, which are concepts that are demonstrated by a system over time. When measuring ecological outcomes, we have to acknowledge that an absolute value for one area may be a poor outcome for one area but a good one in another, depending on many environmental conditions. As a result, it is frequently necessary to develop indicators of ecological outcomes that are normalized by time, via previous measurements within the same system, or by ecologically comparative settings. The DV in this case becomes a comparison between different points in time in one system or between that system and similar systems.
Reliability generally refers to the consistency of the second step just described. Such measurements are generally taken with the aid of a data collection instrument and/or protocol. The implementation of this protocol is ideally highly consistent, or reliable, across distinct implementations. For research that involves many observations this is particularly important because without such reliability we cannot be sure that the measurement of variables on each observation is actually producing consistent and thus comparable data.
This type of validity is only applicable to projects that conduct statistical analyses. It is sometimes confused with internal validity, but is rather distinct. Although internal validity deals with causal inference, statistical conclusion validity deals with conclusions that are made about the actual data. For example, we might examine whether two variables correlate with each other or not and conclude that they do. This is a conclusion whose statistical validity we should concern ourselves with. Whether or not this correlation actually implies a causal relationship between the two is a separate issue, and that is where internal validity comes in. Statistical conclusion validity is frequently determined by the extent to which important assumptions made by statistical methods and models are true. A critical part of a statistical analysis is to test for violations of any such assumptions and to correct for them if possible.
The researcher should not view his or her task as maximizing every one of the criteria discussed above because there are some trade-offs that frequently must be dealt with. Most obviously, there is a trade-off between the feasibility of a project and many of the other criteria because improving a research design and implementation generally involves additional expenses. When considering a way to improve a research project along one of the criteria, researchers should consider what resources would be required and how demanding this would be on the resources available.
Another important relationship to consider is that between internal and ecological validity. One of the most popular discussions of this relationship describes it as a trade-off for the following reason: as we apply increasing amounts of control to minimize variation of the great majority of variables, we increase internal validity essentially by controlling for alternative explanations, but we decrease ecological validity. The more controlled a setting is, the less likely it is to be representative of a real-world setting (lowering ecological validity). Moreover, if we really only allow one independent factor to vary, then deductive validity may be threatened as well because we cannot explore the extent to which additional factors might interact with this variable to affect important outcomes. A factorial design can hypothetically account for all of this, but factorial designs can become very costly to implement if one tries to examine more than one or two interaction effects.
Other than this negative relationship, internal validity is generally increased when a researcher increases measurement, external, and statistical validity. The more external validity there is, the more representative a sample is of a population. If a causal inference is made with respect to the sample, external validity and internal validity become almost the same thing because we are then concerning ourselves with generalizing this causal inference to the population. Measurement validity supports internal validity in the sense that we cannot make valid causal inferences if we do not measure our concepts correctly. Finally, for statistical analyses, the causal inferences we make are based on statistical conclusions, which must be in compliance with the necessary statistical assumptions. When we are conducting inferential statistics, as we usually are, then there is also a similarly positive relationship between statistical and external validity.
It has not been my intent here to promote one particular way of conducting ESS. As mentioned in the introduction, one of the hallmarks of this field is its interdisciplinarity. This is widely accepted as a strength, based on the premise that the complex systems that ESS scholars analyze require the application of multiple methods to be scientifically understood. At the same time, I believe that some of the concepts and issues presented here are faced by many if not most ESS scholars. Such scholars must decide, for example, how much to emphasize deductive vs. inductive approaches in their research and consider the political as well as practical implications of this decision. They need to consider what scientific values (internal validity, external validity) they strive for in their work, and whether they face trade-offs between these. A highly diverse ESS should be compatible with a systematic recording and documenting of that diversity, which is one of the goals that a rubric like this may achieve.
I want to thank Graham Epstein, Louisa Evans, Forrest Fleischman, Gustavo Garcia-Lopez, Michael Schoon, and Andreas Thiel for contributing their thoughts on key areas of this manuscript.
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