Where Are the Seeds of Novelty Found? Surprise, Rereading, and Novelty That Is Only Apparent

Does Changing Your View Make Something New?

Faced with a topic that feels “already done to death,” researchers often think that changing the point of view should bring out novelty. The records that support this expectation are found in a classic of the sociology of science.

In a case Barber and Fox reported in 1958, two medical scientists each came across the same phenomenon in the course of their own research. The ears of rabbits injected with the enzyme papain went limp and, after a while, recovered. One went on from this observation to a discovery; the other did not. Barber and Fox interviewed the two repeatedly and compared how the same chance event turned into a discovery for only one of them. The object was the same; what differed was the one looking.

There is also a record pointing the other way. Grit (a trait said to consist of perseverance of effort and consistency of interest) has been presented as a higher-order trait, distinct from conscientiousness, that predicts success well. In a meta-analysis combining 88 independent samples (66,807 people), Credé, Tynan, and Harms showed that the higher-order structure of grit was not confirmed and that grit correlated very strongly with conscientiousness. The name was new, but much of what it measured overlapped with a known trait.

The same operation of “changing the view” becomes a discovery in one case and ends in merely apparent newness in the other. Where do the paths diverge?

The sister notes have dealt with what comes before and after this point. Where Do Novel Research Questions Come From? The Four Loci and Their Combinations, Examined Against the Literature organized where in a paper novelty resides, How Novelty Is Made and How It Is Claimed: A Typology of Establishing Strategies how novelty is made and how it is claimed, and An Academic Map of Methods for Reframing Problems: From Abduction-2 to Problem Structuring methods for reframing the problem itself. How a Claim of Novelty Is Verified, Defended, and Written: From Pre-Submission Checks to Bundles of Papers dealt with how a claimed novelty is verified and defended before and after submission. What remains is the stage earlier than all of these. Where do researchers notice a seed, and how do they reread a topic that seems already covered? And under what conditions does such rereading end in mere appearance?

Where Do Researchers Pick Up Seeds?

Few studies have followed the sources of ideas over a long period through researchers’ own records. One is the study by Root-Bernstein, Bernstein, and Garnier. They interviewed 40 male scientists (four of whom later won Nobel prizes) four times between 1958 and 1978, and in 1988 sent a questionnaire to the 38 who were still alive. The questions included when significant insights were most likely to come (while working directly on the problem, while working on other problems, while relaxing, while walking). Scientific success correlated with visual thinking, artistic and musical hobbies, and a broad range of avocations. They concluded that successful scientists integrate their research and their activities outside research so that each sustains the other, whereas the outside activities of less successful scientists compete with research for time. Seeds are not picked up only at the desk; how many can be picked up depends on whether activities outside research connect to the research.

Studies that use laboratory notebooks as sources have shown that seeds appear inside ongoing research. Kulkarni and Simon reproduced Hans Krebs’s 1932 discovery of the urea cycle with a program called KEKADA, following the records of his notebooks and interviews. KEKADA reacts to surprises, formulates hypotheses to explain them, and designs experiments to test them. Its behavior was built to match the way of proceeding that the notebooks and interviews show for Krebs. Holmes followed the research pathways of six experimental scientists across three centuries, from Lavoisier to Krebs, Meselson and Stahl, and Benzer, at three scales (broad, middle, and fine), in search of features common to long-term experimental research.

On who tries out new ideas, there are quantitative records. Packalen and Bhattacharya identified new ideas from the text of nearly all biomedical articles published since 1946, and showed that papers by younger researchers are more likely to build on new ideas. The combination of a young first author and an experienced last author tried out new ideas more than any other combination.

There are also studies of organizational conditions. Heinze, Shapira, Rogers, and Senker examined 20 cases of highly creative research accomplishments in nanotechnology and human genetics in Europe and the United States. Creative accomplishments were associated with small group size, organizational contexts with sufficient access to a complementary variety of technical skills, stable research sponsorship, timely access to extramural skills and resources, and facilitating leadership. They point out that increasing competitive research council funding at the expense of flexible institutional sponsorship could be a threat to creative science.

Do People at the Boundary Find More Seeds?

The view that new seeds are easier to find at the boundaries of groups comes with an explanation of the mechanism. According to Burt, opinion and behavior are similar within groups and differ between them. People connected across groups are familiar with other ways of thinking and doing, so they see options others do not see. He examined the networks of 673 managers in the supply chain of a large American electronics company and had two of the company’s executives rate the quality of the best ideas each had written down. The more a person occupied a brokerage position between groups, the more likely they were to voice ideas, the less likely to have ideas dismissed, and the more likely to have them rated as valuable.

Scenes of people from outside a boundary solving problems are also on record. Jeppesen and Lakhani analyzed data on 166 science problems that the laboratories of large R&D-intensive companies broadcast to outsiders, and on more than 12,000 solvers. The farther a solver’s field of expertise was from the field of the problem, the more likely the solver was to produce a winning solution. Female solvers, known to be in the “outer circle” of the scientific establishment, performed significantly better than men.

Still, the proposition that “the more marginal, the more innovative” does not hold in general. Gieryn and Hirsh examined X-ray astronomy in its formative years (1960 to 1975) and showed that marginal scientists were no more likely than others to contribute innovations. They went on to argue that the concept of marginality is so ambiguous as to be almost worthless as a tool for studying the sources of innovation. Being outside alone is also not the same as spanning a boundary. Singh and Fleming analyzed more than half a million patents and showed that lone inventors, especially those without organizational affiliation, are less likely to achieve breakthroughs and more likely to produce particularly poor inventions. Collaboration reduces poor outcomes through selection and increases breakthroughs through opportunities for recombination. Whether broad knowledge helps also depends on the domain. Teodoridis, Bikard, and Vakili used the effect of the Soviet Union’s collapse on theoretical mathematicians as a natural experiment and showed that generalists have the advantage in slow-changing domains and specialists once the pace of change increases.

Seeds found at the boundary can also be discounted by those who receive them. Hofstra and colleagues followed the dissertations and subsequent careers of about 1.2 million people who received doctorates in the United States from 1977 to 2015. Novelty was measured as the number of pairs of concepts first linked in a dissertation, and about half of the new links were never used again. Groups underrepresented by gender and race produced novelty at higher rates. Yet their novel contributions were taken up by other scholars at lower rates, and equally impactful contributions were less likely to lead to success in research careers. Links between semantically distant concepts were taken up less by later research, and students of the underrepresented gender introduced somewhat more distant links. The boundary is a place where seeds are easy to find and, at the same time, a place where the seeds found are hard to get recognized.

In What Forms Does Chance Become a Seed?

Chance discoveries tend to be lumped into a single type. Starting from Merton’s archive (513 boxes), Yaqub gathered 118 examples and divided serendipity into four types.

• Walpolian: discovery of things the discoverer was not in search of. Close to Walpole’s original usage.
• Mertonian: discovery that reaches the solution of a problem that was being sought by an unexpected route.
• Bushian: discovery in which untargeted research (or activity that is not research at all) yields a solution that was not sought.
• Stephanian: discovery in which untargeted research comes upon both a problem no one had yet posed and its solution. It does not help immediately and later solves a problem.

He also identified four mechanisms by which serendipity comes about. Theory-led, in which the growth of theory makes an observation stand out; observer-led, in which something is visible only to observers with particular tools, techniques, or attributes; error-borne, which arises from methodological deviations and errors; and network-emergent, which arises from connections among multiple actors. On error, he introduces the principle Delbrück called “limited sloppiness.” In Luria’s words, somewhat untidy experiments can pay off, provided one is aware of the element of untidiness. Networks bring discoveries to attention and gather the skills needed to exploit them, but they can also make chance harder to see through groupthink.

Chance discoveries disappear once they become papers. Yaqub cites, as one reason serendipitous discoveries are rarely recorded, the fact that papers omit the dead ends of research or work them into tidy narratives, and introduces it as the practice Barber and Fox called “retrospective falsification.” Copeland argues that serendipity should be understood as an emergent property of discovery, describing an oblique relationship between the intentions that drove a discovery process and the outcome obtained. Because the significance of an unexpected observation can only be reflected upon after a valuable outcome has been obtained, serendipity is categorized retrospectively. She also states that recognizing serendipity is correlated with acknowledging the limits of expectations about where knowledge comes from.

Can chance encounters be designed and increased? Lane and colleagues ran a field experiment at a medical research symposium that exogenously varied opportunities for face-to-face encounters among 15,817 pairs of scientists, and followed their publications for the next six years. Pairs that shared some overlapping interests acquired more knowledge when they met and coauthored 1.2 more papers. Pairs from the same field cited each other’s work three to seven times less. For a chance encounter to become a seed, some shared knowledge is needed, and when the field is the same, competitive effects also appear.

At What Moment Does Noticing Happen?

What, then, is happening at the moment one notices a seed? What KEKADA, the reproduction of Krebs, reacted to was surprise. Surprise arises only where there is an expectation. Klahr and Simon compared four approaches (historical accounts, psychological experiments with nonscientists, observation of laboratories, and computational models) through the theory of human problem solving, and argued that their findings converge at key points of the discovery process. KEKADA is an example from the computational-model side.

Qualitative research methodology makes surprise a principle of theory construction. Timmermans and Tavory attributed the scarcity of theoretical innovation from grounded theory in part to its commitment to letting theory emerge inductively. Induction does not logically lead to new theoretical insights. In its place they made abduction, which produces new hypotheses from surprising evidence, the guiding principle. Abduction arises from the researcher’s social and intellectual positions, but it is supported by procedures: revisiting the data, defamiliarization, and alternative casing. Whether one can be surprised depends on what the researcher knows. Glaser, too, argued that generating grounded theory requires developing the skill of theoretical sensitivity, and in the same book devoted chapters to theoretical memos and to their theoretical sorting.

When expectations are too strong, surprise gets discounted. Chinn and Brewer analyzed how scientists and science students respond to anomalous data and distinguished seven forms of response. They are ignoring the data, rejecting them, excluding them from the scope of current theory, holding them in abeyance, reinterpreting them, making peripheral changes to the theory, and changing the theory. Only the last accepts the data and changes the theory; the other six discount the data in some way in order to protect the existing theory. Fugelsang, Stein, Green, and Dunbar observed scientists reasoning live in laboratory meetings. The scientists were at first reluctant to consider data inconsistent with their expectations as “real.” But when the inconsistent data were observed repeatedly, they modified their theories. In a controlled simulation, students followed the same course. Seeds tend at first to be treated as error.

Locke, Golden-Biddle, and Feldman organized clues for getting past this discounting from the side of doubt, which drives Peircean abduction. Their three principles are to turn toward not knowing, to nurture hunches that have not yet become words, and to disrupt the order. In explaining the third principle, they quote a passage from Abbott. If your first reaction on meeting an unusual fact is to jam it into an existing category or to rationalize it in terms of your favorite idea, you will have trouble seeing puzzles.

How Has Design Research Defamiliarized the Familiar?

With objects that are too familiar, surprise itself is hard to come by. Design research and HCI have responded to this with procedures of defamiliarization.

Bell, Blythe, and Sengers argued that the home is so familiar that it must be defamiliarized to open its design space. Home appliances are loaded with cultural meanings that are easy to overlook, such as the gendered division of domestic labor. They offered three narratives of defamiliarization. Reading the history of American kitchens to reconsider new domestic technologies, using an ethnography of an extended household in England to problematize taken-for-granted domestic technologies, and using a comparative ethnography of urban Asia’s middle classes to see new technologies being taken up in unexpected ways. The same topic, the home, turns into new design problems when it is resituated in history, in another form of household, and in another culture.

Sengers, Boehner, David, and Kaye proposed reflective design, which analyzes the unconscious values and assumptions embedded in technology and designs, builds, and evaluates devices that reflect alternative possibilities. Loke and Robertson built a methodology for movement-based interaction design that adds the perspective of the mover to those of the observer and the machine, and made “making strange” its central tactic. Wilde, Vallgårda, and Tomico analyzed methods of embodied design ideation with a framework for understanding and leveraging the power of estrangement. According to Clancey’s review, Winograd and Flores argued that knowledge is not representations in the brain but an unformalized shared background, from which people articulate representations in order to cope with new situations. Computer programs, by contrast, contain only pre-selected objects and properties, so they have no basis for moving beyond the initial formalization when a breakdown occurs.

There are also procedures that defamiliarize from the side of the data. Jiro Kawakita’s KJ method was developed out of difficulties in interpreting ethnographic data from Nepal. Scupin introduces the KJ method as a procedure that builds on Peirce’s notion of abduction and relies on intuitive, non-logical thinking processes. In rearranging fragments to find relations before putting data into existing categories, it is close to Timmermans and Tavory’s revisiting and alternative casing.

How Is a Seemingly Covered Topic Reread?

The literature that collects operations for changing the view is concentrated in psychology and sociology. To correct methodology courses that focus on testing hypotheses and neglect generating them, McGuire organized 49 heuristics for generating hypotheses into 5 categories and 14 subcategories. They range from the commonsense perceptiveness that notices the oddity of natural occurrences to uses of sophisticated quantitative analysis that provoke insight. Taking as his cue Galton’s observation that the same thoughts recur, Wicker grouped strategies for getting new perspectives on familiar research problems into four sets. They are playing with ideas, considering contexts, probing and tinkering with assumptions, and clarifying and systematizing the conceptual framework. Becker presented “tricks” for thinking about research while doing it in four chapters: imagery, sampling, concepts, and logic. Mills wrote that the sociological imagination consists in considerable part of the capacity to shift from one perspective to another, and as ways of stimulating the imagination he listed rearranging the contents of one’s file, playing with the words that define a problem (looking up synonyms), building types, considering extremes and opposites, and seeking comparable cases.

Fiedler gave these operations a position. Theory formation is a cycle of a “loosening” stage that produces variation and a “tightening” stage that selects. Psychology has refined the methodology of the tightening stage, but attempts to understand the loosening stage are conspicuously missing. Operations that change the view belong to the loosening side, and whether they become novelty is decided on the tightening side.

Splitting and Renaming Constructs

Fisher and Aguinis listed seven tactics of theory elaboration, which builds new theoretical insight on preexisting concepts or a preliminary model. They are horizontal contrasting, vertical contrasting, new construct specification, construct splitting, structuring specific relations, structuring sequence relations, and structuring recursive relations. Of these, splitting and new construct specification are operations that give a known phenomenon a new name and boundary.

The meta-analysis of grit is also an example in which the success and failure of this operation diverged within a single study. In the analysis by Credé and colleagues, the view of grit as a single higher-order trait was not supported. On the other hand, the facet “perseverance of effort” had significantly stronger criterion validities than the other facet, “consistency of interest,” and explained academic performance even after controlling for conscientiousness. The claim of a new trait as a whole was close to appearance, while one of the split facets retained a part that the known trait could not explain.

The conditions under which this ends in appearance lie in an old warning from psychometrics. In 1927 Kelley argued that tests of achievement and tests of intelligence measure things that are at least 90 percent the same, yet they are treated as different because their names differ. He named the jangle fallacy: using two words that sound different but in fact cover the same basic situation as though they were truly different. The reverse error, treating different things as one concept merely because they are called by the same word, is called the jingle fallacy, after the name Aikins gave it as reported by Thorndike. Le, Schmidt, Harter, and Lauver asked 292 employees to respond at two times and showed that, once measurement error was corrected, the construct-level correlation between job satisfaction and organizational commitment reached .91, and that both had similar relations with positive and negative affectivity. A distinction well established conceptually could not be told apart empirically. Hodson pointed out that psychology has neglected a mathematical fact, namely that if the correlations within and between indicators are roughly comparable, the latent factors will correlate near-perfectly and be redundant, and proposed calling the problem a “construct redundancy fallacy” rather than using the cute label jingle-jangle. Shaffer, DeGeest, and Li addressed construct proliferation, the accumulation of constructs that look different but may be identical, and set out a procedure for assessing discriminant validity that accounts for three kinds of measurement error. Elson, Hussey, Alsalti, and Arslan took issue with the fact that most psychological measures are used only once or twice, as a threat to the credibility of research. Renaming becomes novelty only when, with measurement error corrected, the construct can be distinguished from existing constructs and explains something they cannot.

Changing the Context

Johns defined context as situational opportunities and constraints that affect the occurrence and meaning of organizational behavior and the functional relationships between variables, and argued that researchers do not sufficiently appreciate its impact. Whetten divided research that borrows theory across contexts into theories in context, which place theory in a context, and theories of context, which theorize the context itself. His examination responds to the criticism that Chinese organizational research relies too heavily on Western theory, and explores ways not to stop borrowing but to make borrowing sensitive to context. He positioned the use of context effects to explain organizational phenomena as an essential contribution to all cross-context scholarship. Tsui pointed out that most global management knowledge comes from research in North America and Western Europe, and argued that high-quality indigenous research in the novel contexts of emerging economies can contribute both contextualized knowledge and global knowledge.

The comparative ethnography by Bell and colleagues can be read as an example in which changing the context produced new design problems. Against the “digital home of the future” envisioned by Western domestic technology design, new technologies were taken up in unexpected ways in the daily lives of urban Asia’s middle classes.

This ends in appearance when an existing theory has merely been applied and confirmed in a new place, without explaining why a difference appears (or does not) in that place. The way of posing questions that Sandberg and Alvesson called application spotting (How Novelty Is Made and How It Is Claimed: A Typology of Establishing Strategies) tends to take this form. In terms of Whetten’s distinction, research that changes the context has novelty when it brings the effects of context into the theory.

Changing the Level of Analysis

Rereading an individual phenomenon as a group or organizational phenomenon has been developed in organizational research as multilevel theory. Klein, Dansereau, and Hall divided the assumptions made when specifying the level of a theory into three (homogeneity within higher-level units, independence from higher-level units, and heterogeneity within higher-level units) and argued that these assumptions influence constructs and propositions as well as data collection, analysis, and interpretation. Chan organized the relations among constructs that refer to the same content but are qualitatively different at different levels (individual, team, organization) into five basic forms of composition models, and held that specifying a composition model is a requirement of multilevel research.

The classic case of the conditions under which this ends in appearance is Robinson. Using the 1930 United States census (the population aged 10 and over), Robinson compared correlations with the individual as the unit with ecological correlations with areas as the unit. The individual correlation between being Black and illiteracy was .203, but with states as the unit it became .773, and with census divisions as the unit, .946. The individual correlation between foreign birth and illiteracy was positive at .118, but the correlation across states was −.526, and across divisions −.619, reversing its sign. Reading a relation found at the group level as a relation among individuals looks like a new finding but becomes an error. Rereading at a different level becomes novelty when it shows how the relation at one level connects to the relation at another (a composition model).

Rereading the Same Data with a Different Procedure

Reading existing data again with a different procedure can change the conclusion. Ebrahim and colleagues searched for studies that reanalyzed individual patient data from published randomized controlled trials to test the same hypothesis, and found 37. The reanalyses differed most often in statistical approach (18) and in the definition or measurement of the outcome (12). Thirteen (35%) reached interpretations different from the original article: 3 concluded that different patients should be treated, 1 that fewer patients should be treated, and 9 that more patients should be treated. Only 5 of the reanalyses, however, were performed by authors entirely independent of the original ones.

A changed conclusion does not by itself mean new knowledge. Silberzahn and colleagues had 61 analysts in 29 teams analyze the same data for the same question (whether soccer referees are more likely to give red cards to players with darker skin). The estimated odds ratios ranged from 0.89 to 2.93 (median 1.31); 20 teams (69%) reported a significant positive effect and 9 teams (31%) a nonsignificant result. The 29 analyses used 21 unique combinations of covariates. This variation could not be explained by the analysts’ prior beliefs, their expertise, or peer ratings of the quality of the analyses. A different result obtained with a different procedure is first suspected of stemming from the choice of procedure. A reanalysis has novelty when it can explain why the difference in procedure changes the conclusion. If the procedure was chosen after seeing the results, it takes the same form as HARKing, discussed in How Novelty Is Made and How It Is Claimed: A Typology of Establishing Strategies.

Checking a Theory by Changing the Operationalization

There is also rereading that tests the same theory again with a different operationalization. Crandall and Sherman contrasted direct replication, carried out as close to the original study as possible, with conceptual replication, which tests the same theoretical process by different methods. Direct replication increases confidence in the operationalization, and conceptual replication increases confidence in the theory. In the example they give, the speed of light that Rømer estimated from discrepancies in the timing of the eclipses of Jupiter’s moon Io did not convince the leading scientists of the day, even though he repeated the same observations for years. The conclusion that the speed of light is finite was accepted when Bradley obtained a similar value by a different method, using shifts in the apparent positions of stars. Reaching the same conclusion with a different instrument was what settled it.

They also examine the conditions under which this ends in appearance. When a conceptual replication fails, the failure tends to be dismissed as a problem with the operationalization rather than with the theory. Critics have called conceptual replication a mechanism that only produces confirmation bias. Crandall and Sherman respond that the same problem confronts failed direct replications, and then propose making failed conceptual replications public and putting them to use. Rereading by changing the operationalization becomes mere repetition of confirmation unless what would count as failure is decided in advance.

Going Back to the Phenomenon Before the Theory

Hambrick argued that because the leading management journals make a contribution to theory a condition of publication, research that observes and reports facts not yet known is shut out. His position is that the collection of facts itself eventually contributes to the development of theory. Von Krogh, Rossi-Lamastra, and Haefliger positioned research that identifies and reports new or recent phenomena as research that establishes the empirical facts and constructs that enable later inquiry to proceed. Using the study of open source software development as an illustration, they set out a sequence of research activities: identification, exploration, design, theorizing, and synthesis. According to them, rigorous phenomenon-based research tackles problems that are relevant to management practice and fall outside the scope of available theories. Theorizing that starts from phenomena was also discussed in Where Do Novel Research Questions Come From? The Four Loci and Their Combinations, Examined Against the Literature through the account of Fisher, Mayer, and Morris.

This ends in appearance when a phenomenon that existing theory can explain is reported as a new phenomenon. The condition for rereading by going back to the phenomenon to become novelty is that the phenomenon lies outside the scope of existing theory.

Defamiliarizing the Familiar

Defamiliarization in design research and the defamiliarization of Timmermans and Tavory are both operations that treat the familiar as unfamiliar again. They resituate what the researcher takes for granted in history, another culture, another body, or another way of casing, and so create the conditions for surprise.

This operation tends to end in appearance when the surprise is new only to the researcher. Because whether one can be surprised depends on the researcher’s intellectual position, what surprises one researcher may already be known in another field. A seed obtained by defamiliarization becomes a candidate for novelty only after it has been checked against the literature of the field (how to check is organized in How a Claim of Novelty Is Verified, Defended, and Written: From Pre-Submission Checks to Bundles of Papers).

Operations and Conditions Side by Side

Apparent Novelty and Overlooked Novelty

Construct redundancy, misreading ecological correlations, and differences due to analytic choices are all failures in which the newness gained by changing the view turns out to have been known or mistaken. The literature records failures in the opposite direction just as often. These are cases in which a real seed is discounted by the person who found it and by those around them.

Researchers themselves are at first reluctant to consider data inconsistent with their expectations as real (Fugelsang et al.). Of the seven responses to anomalous data, six protect the existing theory (Chinn & Brewer). On the receiving side as well, novel contributions from underrepresented groups are taken up less (Hofstra et al.).

Experiments on selecting ideas point in the same direction. Rietzschel, Nijstad, and Stroebe found a strong tendency, when people select ideas, to choose feasible and desirable ideas at the cost of originality. When explicitly instructed to select creative or original ideas, the originality of the chosen ideas rose, but the selectors’ satisfaction and the rated effectiveness of the chosen ideas fell. Mueller, Melwani, and Goncalo showed in two experiments that when a motivation to reduce uncertainty is at work, a negative bias against creative ideas arises and the very ability to recognize a creative idea is impaired. Licuanan, Dailey, and Mumford had 181 undergraduates evaluate teams’ marketing campaigns and showed that the originality of truly novel ideas is underestimated, and that having evaluators actively analyze the originality of the product and the teams’ interactional processes reduces this error.

The expectation that “changing the view will bring out novelty” lies between these two failures. Discount a seed without changing the view, and one overlooks real newness. Change the view without tightening, and one claims apparent newness. Leavitt, Mitchell, and Peterson argued that organizational science leans toward confirmatory testing and that research that bounds and reduces theory (theory pruning) is scarce. In a field crowded with theories and constructs, comparing existing views and reducing them can sometimes be more novel than adding a new view.

How Are Seeds Grown into Questions?

A seed that has been found is not yet a question. It needs the stages of keeping it, letting it rest, talking about it, and choosing.

On keeping, there are studies of scientists’ notebooks. Tweney showed that Faraday’s notebooks are among the largest records left by a major scientist and contain traces of his systematic invention and exploration of recording techniques themselves. The notebooks are also material that reveals the role of memory in scientific thinking. Using Darwin’s notebooks as sources, Gruber described creative work as a network of enterprises proceeding in parallel, and Root-Bernstein and colleagues used the same term to explain what characterizes successful scientists. In the appendix to The Sociological Imagination, Mills wrote that the researcher must set up a file, which is to say, keep a journal. Personal experience and professional activities, studies under way and studies planned, are joined in it. He wrote that one must cling to vague images and notions, if they are one’s own, and work them out, and held that original ideas almost always first appear in such forms.

On letting it rest, there is an accumulation of psychological experiments. Sio and Ormerod meta-analyzed studies of the effect of incubation, setting a problem aside for a while, and confirmed a positive effect. The effect was larger for divergent thinking tasks, which call for many answers, than for linguistic or visual insight problems. The longer the preparation period, the larger the effect, and filling the set-aside period with a high-demand task made the effect smaller. Baird and colleagues showed that, on creativity problems encountered earlier, a group that did an undemanding task during the break improved performance more than groups that did a demanding task, rested, or took no break, and that the improvement was associated with the degree of mind wandering rather than with the amount of explicitly directed thought about the problems. A seed can grow in the time after one has worked on it enough and then let go.

The effect of talking is conditional. Hasan and Koning ran a field experiment at a startup bootcamp and showed that participants high in openness produced better ideas after talking with extroverted peers but worse ideas after talking with introverted ones. Participants low in openness produced mediocre ideas no matter whom they talked with. Boudreau and colleagues randomly assigned researchers at Harvard Medical School to 90-minute structured information-sharing sessions and showed that pairs assigned to the same session were 75% more likely to apply for a grant together. Catalini used the constraints on the allocation of labs imposed by asbestos removal on the Jussieu campus in Paris to show that colocation increases the likelihood of joint research by 3.5 times. Colocated labs grew more similar in topics and in the literature they cited, while separated labs embarked on less correlated research trajectories. Proximity produces collaboration, but it also aligns points of view.

At the stage of choosing, a creator’s eye helps. With data on 339 circus arts professionals and 13,248 audience members, Berg compared forecasts of the success of new acts. Creators forecast the success of others’ novel ideas more accurately than managers, but had no such advantage for their own ideas. In the laboratory study, the creators’ advantage was tied to a role that involves both the divergent thinking of generating ideas and the convergent thinking of evaluating them. Rules of thumb for choosing a good problem (Alon) and the conditions for being “interesting” (Davis) are organized in Where Do Novel Research Questions Come From? The Four Loci and Their Combinations, Examined Against the Literature and How Novelty Is Made and How It Is Claimed: A Typology of Establishing Strategies.

A Procedure for Finding the Seeds of Novelty

Going back to the two records at the beginning, both the medical scientist who pursued the floppy-eared rabbits and the researchers who proposed grit changed their view. The difference lies in what they did after changing it.

1. Write down your expectations first: Write down what you think will happen before you observe. Surprise appears only as a discrepancy from expectation.¹²
2. Record inconsistent data before discarding them: Keep results that do not match your expectations before dismissing them as error, and check whether they recur. Responses that protect the existing theory are more likely.³⁴⁵
3. Connect activities outside research and other topics to your research: Arrange avocations and other research running in parallel so that they sustain your research rather than compete with it for time. Some types of serendipity come from untargeted exploration and from error.⁶⁷
4. Create contacts that span groups: Take positions where you become familiar with other groups’ ways of thinking. People whose interests partly overlap with yours are more likely to lead to knowledge production.⁸⁹¹⁰¹¹
5. Defamiliarize familiar objects: Resituate them in history, another culture, another body, extremes and opposites, and comparable cases, and turn what is taken for granted into a problem. Lists of heuristics are a starting point for getting your hands moving.^122131415
6. Choose one operation of rereading and write in one sentence what you reread as what: Make explicit which you did: split, change the context, change the level, change the procedure, change the operationalization, or go back to the phenomenon.^1617181920
7. Pass the checks for apparent novelty: For renaming, check discriminant validity and incremental explanatory power; for a change of level, the composition model; for a change of context, the explanation of context effects; for a change of procedure, the reason the conclusion changes.^212223242526
8. Keep it, let it rest, and talk about it: Keep even vague ideas in a file. After working on a problem enough, let go of it during low-demand time. For open creators, a conversation partner who shares information helps.^13272829
9. Do not discard originality when choosing: Do not choose seeds by ease of execution alone. When evaluating others’ seeds, borrow a creator’s eye.³⁰³¹³²
10. Check against the field’s literature: Check whether what surprised you is also new to the field, using the procedure in How a Claim of Novelty Is Verified, Defended, and Written: From Pre-Submission Checks to Bundles of Papers.

How far the familiar should be resituated for it to become a seed is not yet settled. Hofstra and colleagues showed that links between semantically distant concepts are taken up less by later research. No means of telling which of the distant links that went untaken were apparent newness and which were overlooked newness was found in this collection.

Gaps in the Collection

• Large-scale surveys of researchers: large surveys asking researchers across many fields where their ideas come from. What was collected here is limited to a study that followed 40 scientists over a long period (Root-Bernstein et al.) and to case studies from the history of science.
• Evaluation of defamiliarization procedures: studies comparing the conditions under which defamiliarization or reflective design in design research led to accepted research contributions.
• Checks for redundancy in conceptual contributions: there are measurement checks for construct redundancy, but procedures for checking whether a “new concept” in qualitative or conceptual research is a paraphrase of an existing one are scarce.
• Tracking seeds: studies that track, in present-day laboratories, how a seed that appears in a notebook becomes the question of a paper. Cases from the history of science (Krebs, Faraday, Darwin) dominate.
• Telling distant links apart: studies that separate, among semantically distant new links, apparent newness from overlooked newness.
• Empirical work on Japanese idea-generation methods: studies that tested the effect of the KJ method in controlled comparisons were not collected.
• LLM support for rereading: studies that have LLMs propose ways of rereading a topic are left to the LLM section of How Novelty Is Made and How It Is Claimed: A Typology of Establishing Strategies and were not collected for this note.

Related Notes

• How Novelty Is Made and How It Is Claimed: A Typology of Establishing Strategies: a typology of strategies for making and claiming novelty; the five levels of assumptions to question and Davis’s inversion patterns are there
• Where Do Novel Research Questions Come From? The Four Loci and Their Combinations, Examined Against the Literature: the sister note that examined where in a paper novelty resides through four loci
• An Academic Map of Methods for Reframing Problems: From Abduction-2 to Problem Structuring: a literature map of methods for reframing the problem itself (abduction-2, problem finding, C-K theory)
• How a Claim of Novelty Is Verified, Defended, and Written: From Pre-Submission Checks to Bundles of Papers: how to verify, defend, and write up the novelty found, before and after submission

Unverified Items

The main claims in the body were written within the range confirmed in the abstract or in the relevant passages of the full text. The following items could not be confirmed, so they were either not used in the body or written with a narrowed scope.

• Barber and Fox (1958) were used only within the scope of the abstract. The names of the two medical scientists and why one did not pursue the observation are not given, because the full text of the original article could not be reached (the publisher page is paywalled and no public PDF could be retrieved) and only secondary accounts could be checked.
• For Zuckerman (1977), the number of laureates interviewed (41 of 56) was confirmed in the publisher’s description, but the account that laureates acquired standards of work under older laureates could be reached only in secondary descriptions and is not used in the body.
• The arguments on problem choice and problem change in Zuckerman (1978) and Gieryn (1978), role hybridization in Ben-David and Collins (1966), and the multilevel discussion in Rousseau (1985) are not used in the body, because their abstracts could not be reached (no abstract in OpenAlex, Semantic Scholar, Crossref, or PubMed).
• Holmes (2004) was used only within the scope of the publisher’s description.
• The three assumptions in Klein, Dansereau, and Hall (1994) were confirmed from the publisher’s abstract as displayed through a search engine (the publisher page could not be reached behind Cloudflare).
• Winograd and Flores (1986) were used only within the scope of Clancey’s review (the ERIC abstract of the technical report version).
• The accounts of surprise and reflection-in-action in Schön (1983) and of seeing a problem in Polanyi (1966) could be confirmed only through secondary quotations and are not used in the body.
• The speed-of-light example in Crandall and Sherman (2016) follows the paper’s account, but the paper dates Rømer’s observations to 1671 and calls Bradley’s method “parallax motion,” which may diverge from the standard history of science. The body gives no year and describes the method as “shifts in the apparent positions of stars.”
• The value of the correlation between grit and conscientiousness in Credé et al. (2017) is not given, because the full text was not checked.
• The proportion of measures reused in Elson et al. (2023) could not be obtained, so the body stays within the qualitative statement of the abstract.
• The number of methods analyzed by Wilde et al. (2017) could not be confirmed, so the body stays within the scope of the abstract.
• The network of enterprise in Gruber (1981) is used within the range confirmed through the bibliographic record and secondary descriptions (the first edition was 1974).
• Unconfirmed items for works recorded only in the corpus and not used in the body (Root-Bernstein et al. 2008, Csikszentmihalyi 1996, Hackett 2005, Van Maanen et al. 2007, Tavory and Timmermans 2014, the body of Becker, Jaccard and Jacoby 2010, Bamberger 2008, Zahra 2007, Block 1995, Gooding 1990, and others) are listed in the corpus’s ## 未検証事項.

References

Sources of Seeds and Research Pathways

• Heinze, T., Shapira, P., Rogers, J. D., Senker, J. M. (2009). Organizational and institutional influences on creativity in scientific research. Research Policy 38(4):610–623. https://doi.org/10.1016/j.respol.2009.01.014
• Holmes, F. L. (2004). Investigative Pathways: Patterns and Stages in the Careers of Experimental Scientists. Yale University Press. ISBN 0-300-10075-2. https://yalebooks.yale.edu/book/9780300100754/investigative-pathways/
• Packalen, M. & Bhattacharya, J. (2019). Age and the trying out of new ideas. Journal of Human Capital 13(2):341–373. https://doi.org/10.1086/703160
• Root-Bernstein, R. S., Bernstein, M., Garnier, H. (1995). Correlations between avocations, scientific style, work habits, and professional impact of scientists. Creativity Research Journal 8(2):115–137. https://doi.org/10.1207/s15326934crj0802_2

Boundaries and Marginality

• Burt, R. S. (2004). Structural holes and good ideas. American Journal of Sociology 110(2):349–399. https://doi.org/10.1086/421787
• Gieryn, T. F. & Hirsh, R. F. (1983). Marginality and innovation in science. Social Studies of Science 13(1):87–106. https://doi.org/10.1177/030631283013001005
• Hofstra, B., Kulkarni, V. V., Munoz-Najar Galvez, S., He, B., Jurafsky, D., McFarland, D. A. (2020). The diversity–innovation paradox in science. PNAS 117(17):9284–9291. https://doi.org/10.1073/pnas.1915378117
• Jeppesen, L. B. & Lakhani, K. R. (2010). Marginality and problem-solving effectiveness in broadcast search. Organization Science 21(5):1016–1033. https://doi.org/10.1287/orsc.1090.0491
• Singh, J. & Fleming, L. (2010). Lone inventors as sources of breakthroughs: myth or reality? Management Science 56(1):41–56. https://doi.org/10.1287/mnsc.1090.1072
• Teodoridis, F., Bikard, M., Vakili, K. (2019). Creativity at the knowledge frontier: the impact of specialization in fast- and slow-paced domains. Administrative Science Quarterly 64(4):894–927. https://doi.org/10.1177/0001839218793384

Serendipity

• Barber, B. & Fox, R. C. (1958). The case of the floppy-eared rabbits: an instance of serendipity gained and serendipity lost. American Journal of Sociology 64(2):128–136. https://doi.org/10.1086/222420
• Copeland, S. (2019). On serendipity in science: discovery at the intersection of chance and wisdom. Synthese 196(6):2385–2406. https://doi.org/10.1007/s11229-017-1544-3
• Lane, J. N., Ganguli, I., Gaulé, P., Guinan, E. C., Lakhani, K. R. (2021). Engineering serendipity: when does knowledge sharing lead to knowledge production? Strategic Management Journal 42(6):1215–1244. https://doi.org/10.1002/smj.3256
• Yaqub, O. (2018). Serendipity: towards a taxonomy and a theory. Research Policy 47(1):169–179. https://doi.org/10.1016/j.respol.2017.10.007

Surprise, Doubt, and Anomalous Data

• Chinn, C. A. & Brewer, W. F. (1993). The role of anomalous data in knowledge acquisition: a theoretical framework and implications for science instruction. Review of Educational Research 63(1):1–49. https://doi.org/10.3102/00346543063001001
• Fugelsang, J. A., Stein, C. B., Green, A. E., Dunbar, K. N. (2004). Theory and data interactions of the scientific mind: evidence from the molecular and the cognitive laboratory. Canadian Journal of Experimental Psychology 58(2):86–95. https://doi.org/10.1037/h0085799
• Glaser, B. G. (1978). Theoretical Sensitivity: Advances in the Methodology of Grounded Theory. Sociology Press. https://www.sociologypress.com/books/classic_series/theoretical_sensitivity.htm
• Klahr, D. & Simon, H. A. (1999). Studies of scientific discovery: complementary approaches and convergent findings. Psychological Bulletin 125(5):524–543. https://doi.org/10.1037/0033-2909.125.5.524
• Kulkarni, D. & Simon, H. A. (1988). The processes of scientific discovery: the strategy of experimentation. Cognitive Science 12(2):139–175. https://doi.org/10.1207/s15516709cog1202_1
• Locke, K., Golden-Biddle, K., Feldman, M. S. (2008). Perspective: making doubt generative: rethinking the role of doubt in the research process. Organization Science 19(6):907–918. https://doi.org/10.1287/orsc.1080.0398
• Timmermans, S. & Tavory, I. (2012). Theory construction in qualitative research: from grounded theory to abductive analysis. Sociological Theory 30(3):167–186. https://doi.org/10.1177/0735275112457914

Defamiliarization in Design Research and the KJ Method

• Bell, G., Blythe, M., Sengers, P. (2005). Making by making strange: defamiliarization and the design of domestic technologies. ACM Transactions on Computer-Human Interaction 12(2):149–173. https://doi.org/10.1145/1067860.1067862
• Clancey, W. J. (1987). [Review of] Understanding computers and cognition: a new foundation for design. Artificial Intelligence 31(2):232–250. https://doi.org/10.1016/0004-3702(87)90025-7 (technical report version: ERIC ED299966, https://eric.ed.gov/?id=ED299966)
• Kawakita, J. (1967). Hassōhō: Sōzōsei kaihatsu no tame ni [Idea generation: for developing creativity]. Chūkō Shinsho. Chūōkōronsha. https://www.chuko.co.jp/shinsho/2017/06/180136.html
• Loke, L. & Robertson, T. (2013). Moving and making strange: an embodied approach to movement-based interaction design. ACM Transactions on Computer-Human Interaction 20(1):Article 7. https://doi.org/10.1145/2442106.2442113
• Scupin, R. (1997). The KJ method: a technique for analyzing data derived from Japanese ethnology. Human Organization 56(2):233–237. https://doi.org/10.17730/humo.56.2.x335923511444655
• Sengers, P., Boehner, K., David, S., Kaye, J. (2005). Reflective design. Proc. 4th Decennial Conference on Critical Computing, 49–58. https://doi.org/10.1145/1094562.1094569
• Wilde, D., Vallgårda, A., Tomico, O. (2017). Embodied design ideation methods: analysing the power of estrangement. Proc. CHI 2017, 5158–5170. https://doi.org/10.1145/3025453.3025873
• Winograd, T. & Flores, F. (1986). Understanding Computers and Cognition: A New Foundation for Design. Ablex. ISBN 0-89391-050-3.

Heuristics for Rereading

• Becker, H. S. (1998). Tricks of the Trade: How to Think about Your Research While You’re Doing It. University of Chicago Press. ISBN 978-0-226-04124-7. https://press.uchicago.edu/ucp/books/book/chicago/T/bo3683418.html
• Fiedler, K. (2004). Tools, toys, truisms, and theories: some thoughts on the creative cycle of theory formation. Personality and Social Psychology Review 8(2):123–131. https://doi.org/10.1207/s15327957pspr0802_5
• McGuire, W. J. (1997). Creative hypothesis generating in psychology: some useful heuristics. Annual Review of Psychology 48:1–30. https://doi.org/10.1146/annurev.psych.48.1.1
• Mills, C. W. (1959). The Sociological Imagination. Oxford University Press. Public version of the appendix “On Intellectual Craftsmanship”: https://webdelprofesor.ula.ve/humanidades/contrera/cwmills-intel_craft.pdf
• Wicker, A. W. (1985). Getting out of our conceptual ruts: strategies for expanding conceptual frameworks. American Psychologist 40(10):1094–1103. https://doi.org/10.1037/0003-066X.40.10.1094

Theory Elaboration, Context, and Levels

• Chan, D. (1998). Functional relations among constructs in the same content domain at different levels of analysis: a typology of composition models. Journal of Applied Psychology 83(2):234–246. https://doi.org/10.1037/0021-9010.83.2.234
• Fisher, G. & Aguinis, H. (2017). Using theory elaboration to make theoretical advancements. Organizational Research Methods 20(3):438–464. https://doi.org/10.1177/1094428116689707
• Johns, G. (2006). The essential impact of context on organizational behavior. Academy of Management Review 31(2):386–408. https://doi.org/10.5465/amr.2006.20208687
• Klein, K. J., Dansereau, F., Hall, R. J. (1994). Levels issues in theory development, data collection, and analysis. Academy of Management Review 19(2):195–229. https://doi.org/10.5465/amr.1994.9410210745
• Robinson, W. S. (1950). Ecological correlations and the behavior of individuals. American Sociological Review 15(3):351–357. https://doi.org/10.2307/2087176
• Tsui, A. S. (2004). Contributing to global management knowledge: a case for high quality indigenous research. Asia Pacific Journal of Management 21(4):491–513. https://doi.org/10.1023/B:APJM.0000048715.35108.a7
• Whetten, D. A. (2009). An examination of the interface between context and theory applied to the study of Chinese organizations. Management and Organization Review 5(1):29–55. https://doi.org/10.1111/j.1740-8784.2008.00132.x

Replication, Reanalysis, and Phenomenon-Based Research

• Crandall, C. S. & Sherman, J. W. (2016). On the scientific superiority of conceptual replications for scientific progress. Journal of Experimental Social Psychology 66:93–99. https://doi.org/10.1016/j.jesp.2015.10.002
• Ebrahim, S., Sohani, Z. N., Montoya, L., Agarwal, A., Thorlund, K., Mills, E. J., Ioannidis, J. P. A. (2014). Reanalyses of randomized clinical trial data. JAMA 312(10):1024–1032. https://doi.org/10.1001/jama.2014.9646
• Hambrick, D. C. (2007). The field of management’s devotion to theory: too much of a good thing? Academy of Management Journal 50(6):1346–1352. https://doi.org/10.5465/amj.2007.28166119
• Silberzahn, R., Uhlmann, E. L., Martin, D. P., et al. (2018). Many analysts, one data set: making transparent how variations in analytic choices affect results. Advances in Methods and Practices in Psychological Science 1(3):337–356. https://doi.org/10.1177/2515245917747646
• von Krogh, G., Rossi-Lamastra, C., Haefliger, S. (2012). Phenomenon-based research in management and organisation science: when is it rigorous and does it matter? Long Range Planning 45(4):277–298. https://doi.org/10.1016/j.lrp.2012.05.001

Construct Redundancy and Theory Pruning

• Credé, M., Tynan, M. C., Harms, P. D. (2017). Much ado about grit: a meta-analytic synthesis of the grit literature. Journal of Personality and Social Psychology 113(3):492–511. https://doi.org/10.1037/pspp0000102
• Elson, M., Hussey, I., Alsalti, T., Arslan, R. C. (2023). Psychological measures aren’t toothbrushes. Communications Psychology 1:25. https://doi.org/10.1038/s44271-023-00026-9
• Hodson, G. (2021). Construct jangle or construct mangle? Thinking straight about (nonredundant) psychological constructs. Journal of Theoretical Social Psychology 5(4):576–590. https://doi.org/10.1002/jts5.120
• Kelley, T. L. (1927). Interpretation of Educational Measurements. World Book Company. Public version: https://gwern.net/doc/iq/1927-kelley-interpretationofeducationalmeasurements.pdf
• Le, H., Schmidt, F. L., Harter, J. K., Lauver, K. J. (2010). The problem of empirical redundancy of constructs in organizational research: an empirical investigation. Organizational Behavior and Human Decision Processes 112(2):112–125. https://doi.org/10.1016/j.obhdp.2010.02.003
• Leavitt, K., Mitchell, T. R., Peterson, J. (2010). Theory pruning: strategies to reduce our dense theoretical landscape. Organizational Research Methods 13(4):644–667. https://doi.org/10.1177/1094428109345156
• Shaffer, J. A., DeGeest, D., Li, A. (2016). Tackling the problem of construct proliferation: a guide to assessing the discriminant validity of conceptually related constructs. Organizational Research Methods 19(1):80–110. https://doi.org/10.1177/1094428115598239

Keeping, Incubating, Talking About, and Selecting Seeds

• Baird, B., Smallwood, J., Mrazek, M. D., Kam, J. W. Y., Franklin, M. S., Schooler, J. W. (2012). Inspired by distraction: mind wandering facilitates creative incubation. Psychological Science 23(10):1117–1122. https://doi.org/10.1177/0956797612446024
• Berg, J. M. (2016). Balancing on the creative highwire: forecasting the success of novel ideas in organizations. Administrative Science Quarterly 61(3):433–468. https://doi.org/10.1177/0001839216642211
• Boudreau, K. J., Brady, T., Ganguli, I., Gaulé, P., Guinan, E., Hollenberg, A., Lakhani, K. R. (2017). A field experiment on search costs and the formation of scientific collaborations. Review of Economics and Statistics 99(4):565–576. https://doi.org/10.1162/REST_a_00676
• Catalini, C. (2018). Microgeography and the direction of inventive activity. Management Science 64(9):4348–4364. https://doi.org/10.1287/mnsc.2017.2798
• Gruber, H. E. (1981). Darwin on Man: A Psychological Study of Scientific Creativity (2nd ed.; 1st ed. 1974). University of Chicago Press. ISBN 0-226-31007-8.
• Hasan, S. & Koning, R. (2019). Conversations and idea generation: evidence from a field experiment. Research Policy 48(9):103811. https://doi.org/10.1016/j.respol.2019.103811
• Licuanan, B. F., Dailey, L. R., Mumford, M. D. (2007). Idea evaluation: error in evaluating highly original ideas. Journal of Creative Behavior 41(1):1–27. https://doi.org/10.1002/j.2162-6057.2007.tb01279.x
• Mueller, J. S., Melwani, S., Goncalo, J. A. (2012). The bias against creativity: why people desire but reject creative ideas. Psychological Science 23(1):13–17. https://doi.org/10.1177/0956797611421018
• Rietzschel, E. F., Nijstad, B. A., Stroebe, W. (2010). The selection of creative ideas after individual idea generation: choosing between creativity and impact. British Journal of Psychology 101(1):47–68. https://doi.org/10.1348/000712609X414204
• Sio, U. N. & Ormerod, T. C. (2009). Does incubation enhance problem solving? A meta-analytic review. Psychological Bulletin 135(1):94–120. https://doi.org/10.1037/a0014212
• Tweney, R. D. (1991). Faraday’s notebooks: the active organization of creative science. Physics Education 26(5):301–306. https://doi.org/10.1088/0031-9120/26/5/008

Footnotes

1. Kulkarni, D. & Simon, H. A. (1988). The processes of scientific discovery: the strategy of experimentation. Cognitive Science 12(2):139–175. https://doi.org/10.1207/s15516709cog1202_1 ↩

2. Timmermans, S. & Tavory, I. (2012). Theory construction in qualitative research: from grounded theory to abductive analysis. Sociological Theory 30(3):167–186. https://doi.org/10.1177/0735275112457914 ↩ ↩²

3. Chinn, C. A. & Brewer, W. F. (1993). The role of anomalous data in knowledge acquisition: a theoretical framework and implications for science instruction. Review of Educational Research 63(1):1–49. https://doi.org/10.3102/00346543063001001 ↩

4. Fugelsang, J. A., Stein, C. B., Green, A. E., Dunbar, K. N. (2004). Theory and data interactions of the scientific mind: evidence from the molecular and the cognitive laboratory. Canadian Journal of Experimental Psychology 58(2):86–95. https://doi.org/10.1037/h0085799 ↩

5. Locke, K., Golden-Biddle, K., Feldman, M. S. (2008). Perspective: making doubt generative: rethinking the role of doubt in the research process. Organization Science 19(6):907–918. https://doi.org/10.1287/orsc.1080.0398 ↩

6. Root-Bernstein, R. S., Bernstein, M., Garnier, H. (1995). Correlations between avocations, scientific style, work habits, and professional impact of scientists. Creativity Research Journal 8(2):115–137. https://doi.org/10.1207/s15326934crj0802_2 ↩

7. Yaqub, O. (2018). Serendipity: towards a taxonomy and a theory. Research Policy 47(1):169–179. https://doi.org/10.1016/j.respol.2017.10.007 ↩

8. Burt, R. S. (2004). Structural holes and good ideas. American Journal of Sociology 110(2):349–399. https://doi.org/10.1086/421787 ↩

9. Jeppesen, L. B. & Lakhani, K. R. (2010). Marginality and problem-solving effectiveness in broadcast search. Organization Science 21(5):1016–1033. https://doi.org/10.1287/orsc.1090.0491 ↩

10. Lane, J. N., Ganguli, I., Gaulé, P., Guinan, E. C., Lakhani, K. R. (2021). Engineering serendipity: when does knowledge sharing lead to knowledge production? Strategic Management Journal 42(6):1215–1244. https://doi.org/10.1002/smj.3256 ↩

11. Boudreau, K. J., Brady, T., Ganguli, I., Gaulé, P., Guinan, E., Hollenberg, A., Lakhani, K. R. (2017). A field experiment on search costs and the formation of scientific collaborations. Review of Economics and Statistics 99(4):565–576. https://doi.org/10.1162/REST_a_00676 ↩

12. Bell, G., Blythe, M., Sengers, P. (2005). Making by making strange: defamiliarization and the design of domestic technologies. ACM Transactions on Computer-Human Interaction 12(2):149–173. https://doi.org/10.1145/1067860.1067862 ↩

13. Mills, C. W. (1959). The Sociological Imagination, Appendix “On Intellectual Craftsmanship”. Oxford University Press. Public version of the appendix: https://webdelprofesor.ula.ve/humanidades/contrera/cwmills-intel_craft.pdf ↩ ↩²

14. Wicker, A. W. (1985). Getting out of our conceptual ruts: strategies for expanding conceptual frameworks. American Psychologist 40(10):1094–1103. https://doi.org/10.1037/0003-066X.40.10.1094 ↩

15. McGuire, W. J. (1997). Creative hypothesis generating in psychology: some useful heuristics. Annual Review of Psychology 48:1–30. https://doi.org/10.1146/annurev.psych.48.1.1 ↩

16. Fisher, G. & Aguinis, H. (2017). Using theory elaboration to make theoretical advancements. Organizational Research Methods 20(3):438–464. https://doi.org/10.1177/1094428116689707 ↩

17. Whetten, D. A. (2009). An examination of the interface between context and theory applied to the study of Chinese organizations. Management and Organization Review 5(1):29–55. https://doi.org/10.1111/j.1740-8784.2008.00132.x ↩

18. Chan, D. (1998). Functional relations among constructs in the same content domain at different levels of analysis: a typology of composition models. Journal of Applied Psychology 83(2):234–246. https://doi.org/10.1037/0021-9010.83.2.234 ↩

19. Crandall, C. S. & Sherman, J. W. (2016). On the scientific superiority of conceptual replications for scientific progress. Journal of Experimental Social Psychology 66:93–99. https://doi.org/10.1016/j.jesp.2015.10.002 ↩

20. von Krogh, G., Rossi-Lamastra, C., Haefliger, S. (2012). Phenomenon-based research in management and organisation science: when is it rigorous and does it matter? Long Range Planning 45(4):277–298. https://doi.org/10.1016/j.lrp.2012.05.001 ↩

21. Kelley, T. L. (1927). Interpretation of Educational Measurements. World Book Company, pp. 62–65. Public version: https://gwern.net/doc/iq/1927-kelley-interpretationofeducationalmeasurements.pdf ↩

22. Le, H., Schmidt, F. L., Harter, J. K., Lauver, K. J. (2010). The problem of empirical redundancy of constructs in organizational research: an empirical investigation. Organizational Behavior and Human Decision Processes 112(2):112–125. https://doi.org/10.1016/j.obhdp.2010.02.003 ↩

23. Shaffer, J. A., DeGeest, D., Li, A. (2016). Tackling the problem of construct proliferation: a guide to assessing the discriminant validity of conceptually related constructs. Organizational Research Methods 19(1):80–110. https://doi.org/10.1177/1094428115598239 ↩

24. Credé, M., Tynan, M. C., Harms, P. D. (2017). Much ado about grit: a meta-analytic synthesis of the grit literature. Journal of Personality and Social Psychology 113(3):492–511. https://doi.org/10.1037/pspp0000102 ↩

25. Robinson, W. S. (1950). Ecological correlations and the behavior of individuals. American Sociological Review 15(3):351–357. https://doi.org/10.2307/2087176 ↩

26. Silberzahn, R. et al. (2018). Many analysts, one data set: making transparent how variations in analytic choices affect results. Advances in Methods and Practices in Psychological Science 1(3):337–356. https://doi.org/10.1177/2515245917747646 ↩

27. Sio, U. N. & Ormerod, T. C. (2009). Does incubation enhance problem solving? A meta-analytic review. Psychological Bulletin 135(1):94–120. https://doi.org/10.1037/a0014212 ↩

28. Baird, B., Smallwood, J., Mrazek, M. D., Kam, J. W. Y., Franklin, M. S., Schooler, J. W. (2012). Inspired by distraction: mind wandering facilitates creative incubation. Psychological Science 23(10):1117–1122. https://doi.org/10.1177/0956797612446024 ↩

29. Hasan, S. & Koning, R. (2019). Conversations and idea generation: evidence from a field experiment. Research Policy 48(9):103811. https://doi.org/10.1016/j.respol.2019.103811 ↩

30. Rietzschel, E. F., Nijstad, B. A., Stroebe, W. (2010). The selection of creative ideas after individual idea generation: choosing between creativity and impact. British Journal of Psychology 101(1):47–68. https://doi.org/10.1348/000712609X414204 ↩

31. Mueller, J. S., Melwani, S., Goncalo, J. A. (2012). The bias against creativity: why people desire but reject creative ideas. Psychological Science 23(1):13–17. https://doi.org/10.1177/0956797611421018 ↩

32. Berg, J. M. (2016). Balancing on the creative highwire: forecasting the success of novel ideas in organizations. Administrative Science Quarterly 61(3):433–468. https://doi.org/10.1177/0001839216642211 ↩