There's a particular kind of discomfort that comes with genuinely liking your own theory, the kind that's much easier to notice in someone else's work than in your own. I noticed it in myself early in this research — a small, seductive pull toward picking case countries that would probably confirm what I already believed about Brand Drift, and toward quietly steering past the ones that might not. I want to describe how I caught myself doing that, and why I built my entire country selection around actively resisting it instead.
The comfortable version of this research I almost built
If I'd let instinct alone guide my country selection, I likely would have picked three markets that all shared a similar profile to the ones I already understood best — Gulf states, or Gulf-adjacent markets, with broadly similar relational trust economies, broadly similar collectivist orientations, and broadly similar patterns of rapid AI adoption. That version of the research would have been easier to write, faster to defend in a room full of people who already share my starting assumptions, and, I'm fairly convinced now, considerably less trustworthy as a piece of scholarship. A theory that's only ever been tested against contexts similar to the one it was built in hasn't actually been tested at all in any sense a skeptical reader should trust. It's been rehearsed.
What actually counts as a disconfirming case, and why it's harder to pick than it sounds
Critical realism, the philosophical stance underneath my methodology, doesn't just permit looking for a case that might disprove your own theory — it treats doing so as part of what makes an account of a real, structural mechanism credible rather than merely plausible. But "go find a disconfirming case" is easier to say than to actually do, because the natural instinct, even once you've committed to the exercise, is to define "disconfirming" narrowly enough that you can still expect to pass the test. I noticed myself doing exactly this in an early draft of my research design, where I'd shortlisted a country that was culturally different from the Gulf states in some respects but still shared the same rapid, top-down, government-led AI adoption pattern my framework was already built around — which meant it would have tested a different cultural variable while quietly holding the adoption-speed variable constant, protecting my theory from the test I actually needed to run.
Why Estonia, specifically, earned the harder version of that test
Estonia forced me to abandon that comfortable half-measure. It isn't just culturally distinct from the Gulf states — lower power distance, more individualist, a fundamentally different historical relationship to state authority, shaped by decades under Soviet rule followed by a deliberate, rapid pivot toward digital self-governance after independence. It also arrived at its current relationship with automated systems through a genuinely different route: not a recent, headline-driven national AI strategy competing for global attention, but a decades-long, quietly accumulated culture of building transparent, auditable digital infrastructure that predates the current AI moment entirely, embedded in ordinary civic life rather than announced as an ambition. If Brand Drift's underlying mechanism — production and adoption speed outrunning built oversight — only explains what happens in fast, headline-driven, top-down adoption environments, Estonia is close to the best available test of that limit, because it changes multiple variables at once rather than conveniently holding my favorite one constant.
What I was actually afraid the test would show, and why I ran it anyway
I want to be honest about the specific fear underneath this, because I think naming it is more useful than pretending the exercise was purely dispassionate. My real worry wasn't that Brand Drift as a phenomenon wouldn't exist in Estonia at all — some version of the gap between stated identity and automated output seemed likely to show up almost anywhere. My worry was narrower and, I think, more dangerous to a research program if left unexamined: that the specific mechanism I'd built my framework around, oversight failing to keep pace with adoption speed, might turn out to be a Gulf-specific and Morocco-specific story, true in the contexts where I happened to have the most direct personal and professional exposure, and simply inapplicable to a culture built on a fundamentally different relationship to transparency and state trust. That would have meant I'd built a description of a place, dressed up in the language of a general theory — exactly the failure mode critical realism's judgmental rationality is supposed to guard against, and exactly the failure mode I couldn't have caught by only ever picking comfortable cases.
Why running the test mattered more than passing it
I don't think the value of choosing Estonia depends entirely on my framework surviving contact with it cleanly, and I want to resist the temptation to write this piece as though the ending were already triumphant. The value is in having actually run a test capable of failing, rather than one quietly designed to succeed. A researcher who only ever tests a theory against friendly cases can produce work that looks rigorous and isn't, because rigor lives in the willingness to be wrong publicly, not in the volume of confirming evidence gathered from contexts too similar to the original to ever meaningfully disagree.
What almost made it into the shortlist instead
I think it's worth naming, concretely, what my early comfortable shortlist actually looked like, because the specifics make the failure mode easier to recognize in your own work rather than just accepting my abstract description of it. Alongside the Gulf states and Morocco, I'd initially considered a Southeast Asian market with its own rapid, state-encouraged AI adoption program — genuinely different in language, religion, and regional history from anything else in my design, which felt, on first pass, like more than enough difference to count as a real test. It took an uncomfortably long conversation with a colleague, who asked me directly what my framework actually predicted would differ about that case versus my existing cases, for me to realize my honest answer was: not much, on the one variable that mattered most. The adoption-speed mechanism would likely look nearly identical, because the underlying condition producing it — ambitious, top-down, government-encouraged rapid deployment — was the same condition, just wearing a different flag. Geographic and linguistic distance had quietly stood in for genuine variable distance, which is exactly the kind of substitution a comfortable case selection process tends to produce without anyone noticing it happened.
How I'd describe the difference between a "different" case and a genuinely disconfirming one
The distinction I eventually landed on, and the one I'd now recommend to anyone building a comparative research design of their own, is this: a case is genuinely disconfirming only if you can name, in advance, the specific prediction your theory makes that this case could plausibly falsify — not just a general sense that the case "feels different" from your other ones. For my own framework, that meant naming the prediction explicitly before selecting Estonia: if oversight failing to keep pace with adoption speed is truly the mechanism producing Brand Drift, then a context with a fundamentally different, much slower-building, less headline-driven relationship to automated systems should show either a different drift pattern entirely, or none of the pattern at all. That's a prediction specific enough to actually fail, which is precisely what made Estonia worth choosing over a case that merely looked exotic on the surface while quietly sharing my framework's most load-bearing assumption underneath.
The discipline I'm trying to build into every case I pick from here on
Going forward, I've tried to turn this into an actual habit rather than a one-time gesture: for every new case I consider adding to this research, I ask which specific variable in my framework that case would leave untested if I picked it, and I deliberately favor whichever candidate leaves the fewest of my own assumptions safely unexamined. It's a slower, more uncomfortable way to build a research portfolio than picking cases that confirm what I already suspect, and it means occasionally discovering that a case I was genuinely excited about doesn't actually test anything new. I think it's the only version of this work actually worth building, and the only version I'd feel comfortable defending in front of someone who'd read every case as closely as I have.
If you're building a framework, a strategy, or a research design and haven't yet asked what case would most threaten your own assumptions, that's a conversation worth having before you publish, not after. Get Your Free Brand Audit →
References
Bhaskar, R. (1975). A Realist Theory of Science. Leeds Books.
Fletcher, A. J. (2017). Applying critical realism in qualitative research: Methodology meets method. International Journal of Social Research Methodology, 20(2), 181–194.
Hofstede, G. (2001). Culture's Consequences: Comparing Values, Behaviors, Institutions, and Organizations Across Nations (2nd ed.). Sage Publications.