How Two Experiments Separated Skills from Opportunity
This chapter reconstructs how the Georgian study turned a broad question—why interested small firms were not selling online—into comparisons that could speak to different causes. The key distinction is between an intervention that tries to lower the cost of capability and one that makes the benefit of acting immediate. Understanding the assignment, take-up, overlap, and outcome measures lets readers interpret the later results as evidence about particular barriers rather than as a simple contest between a course and an incentive.
One sample tested whether lowering the entry cost was enough
The first experiment was built around a straightforward explanation for low digital participation: firms might want to use online markets but lack the know-how to do so. In 2018, researchers used business-census information from six regions of Georgia to survey firms that indicated interest in e-commerce training. The initial survey reached 567 such firms. After the baseline, an online registration portal brought in another 291 businesses that also registered interest. Together, the 858 firms were randomly assigned either to a pure control group of 220 or to a treatment group of 638 that received the training offer.
The numbers describe a comparison, not a list of program participants. A control firm did not serve as an inferior version of the treatment firm; it supplied the counterfactual question: what would have happened to a similar interested business without the offer? Because assignment was random, systematic differences in motivation, existing digital habits, sector, or managerial ability should be distributed across the groups on average. A later difference in measured digital engagement can therefore be connected to assignment more credibly than a difference between firms that volunteered for training and firms that did not.
That logic applies to the offer, not automatically to attendance. The study estimates an intention-to-treat effect: the average difference created by being assigned to the training group. Only about 56% of firms assigned to treatment actually attended. This is not a flaw to hide, nor does it make the experiment useless. It tells us that the program had two possible points of influence. It could affect behavior by teaching firms, but it could also fail to reach many firms because the act of attending required time, travel, and prioritization. The assignment estimate captures the effect of placing the opportunity in front of the firm under real conditions, including that friction.
For a reader, this is an important separation. “The training did not change adoption” can mean that the material did not help those who attended, that too few attended for the offer to matter at the population level, or that skills were not the binding constraint in the first place. The intention-to-treat result alone cannot identify which of those stories explains every non-adopter. It does, however, answer a practical policy question: what happened when this training offer was made available to these interested Georgian firms?
The first experiment also had a time dimension. Training was delivered between 2018 and 2019, and the 2021 survey served as a follow-up for the training intervention. The researchers measured an e-commerce engagement index rather than relying on a single indicator. The index combined several forms of digital activity, such as selling online, business internet use, online banking, social-media or platform presence, a website, business email, and online marketing. The purpose was to reduce the risk of finding an isolated result simply because many outcomes were tested. It also means that “digital engagement” is a broader construct than a completed online order.
A later survey in 2025 extended the horizon. That extension matters because training is supposed to create knowledge that remains available after the course ends. In the study’s framework, a demand shock is temporary, while human capital could lower the cost of adoption over many future periods. A training effect that appeared only after firms had time to act would therefore be relevant, even if the immediate follow-up were quiet. Conversely, no change years later would make a simple delayed-adoption story less persuasive.
The structure of the first experiment thus separates three events that are often blurred together: a firm was offered training, a firm attended training, and a firm changed its digital behavior. Only the first is assigned by the experiment. The others are outcomes or intermediate responses. Keeping those events separate protects the causal interpretation when the study turns to its second experiment.
A later sample tested whether a concrete opportunity changed the calculation
The demand-side experiment asked a different question. Perhaps firms could learn the mechanics of digital commerce, but did not see a reason to invest the time until an actual buyer appeared. The experiment took place after the training phase. From the original 858 firms, researchers selected businesses that had completed the 2021 follow-up, were still operating, and had goods or services available during the planned intervention. That process produced 205 eligible firms. A further 78 eligible businesses that had not been in the original training experiment were added, creating a demand sample of 283 firms.
Those selection rules are part of what the result means. The demand experiment does not describe every business that once expressed interest. It concerns firms still operating and able to supply something at the time of the intervention, plus a top-up group that met the same eligibility criteria. A firm with a seasonal product unavailable during the intervention period, for example, was not in the relevant risk set. This makes the test more focused on whether an operating firm could respond to an opportunity, but it narrows generalization.
The 283 firms were randomized into three groups: 131 control firms, 76 offered a low demand shock, and 76 offered a high demand shock. Assignment was stratified by three levels of self-reported willingness or propensity to sell online. High-propensity firms had already indicated interest and had some kind of online profile. Medium-propensity firms had indicated interest but did not yet have an online presence. Low-propensity firms reported that they were not interested in selling online. Stratification does not make these permanent categories. It ensures that the study can compare the intervention across starting positions that are relevant to the adoption decision.
The two offers also created a mechanism test. The low demand shock was valued at about $130, roughly the cost of the e-commerce training. The high shock was $780, six times as large. The offer was conditional: the research partner would place an order only if the firm could make the purchase possible online. Firms had two weeks to create a profile with basic business and product or service information and to support a noncash payment and fulfillment path. This was not an unconditional cash transfer. The money represented a prospective order whose value could be realized only after the firm completed the online work.
That distinction changes the interpretation of the comparison. If the main obstacle were a financial fixed cost, a sixfold increase in the prospective order should have made adoption substantially more attractive. If a modest profit and a deadline were enough to push some firms past a threshold, the larger offer might add little. The experiment therefore varies not only whether a firm receives an opportunity, but how strongly the financial return is increased while the work of acting remains.
The demand sample also provides a bridge back to the training experiment. Of the 283 firms, 205 came from the earlier randomized sample. This overlap allows the researchers to ask whether previous training changed a firm’s response to the later order. In intuitive terms, training might make the demand shock easier to use: a firm that already understood the digital process would need less effort to take advantage of the buyer. If the two interventions address complementary parts of one bottleneck, firms receiving both could respond more than firms receiving either one alone.
But the overlap should not be treated as a perfectly simultaneous two-by-two experiment. The training and demand interventions occurred at different times. Firms had to remain eligible for the later sample, and the top-up firms were not part of the original training randomization. The overlap is still valuable because it supplies a structured comparison of prior training and later demand, but it does not erase the selection and timing that define the comparison.
The outcome sits downstream of several decisions
Both experiments become easier to interpret when the path from assignment to outcome is made explicit. Assignment creates an opportunity. The firm then decides whether to attend, prepare, or respond. The researchers observe a measure of digital engagement or a completed online transaction. Each arrow contains behavior that the treatment may or may not change.
For training, the sequence is roughly: assignment to the offer, attendance, exposure to instruction, and later digital activity. A null result at the end of that sequence could arise because attendance was incomplete or because instruction did not change the relevant decision. For demand, the sequence is: assignment to a conditional order, construction of an online profile and payment path, fulfillment of the order, and—if the channel remains useful—later activity. The demand intervention makes the final behavior more immediate, but it does not guarantee that the firm will find repeat customers afterward.
The study’s measurements reflect these differences. In the short run, monitoring records whether the research team could find the firm online and place an order. That is closer to an operational test than a statement of intention: the firm had to make the channel usable. For training, the e-commerce index aggregates several indicators of engagement. In the 2025 endline, the demand outcome is based on what firms reported about selling online or receiving online orders in the relevant period. The long-run measure is therefore not identical to the short-run test.
This is not a technical footnote. If the outcome changes, we need to know what changed. A profile that exists but cannot accept an order is not the same as a functioning sales channel. A successful one-time order is not the same as recurring market participation. And a self-reported online sale years later is not measured in exactly the same way as a research team’s ability to place an order during a two-week intervention. The design can still tell us a great deal, but its claims must stay attached to the outcome actually observed.
The follow-up schedule provides another boundary. The 2021 survey was both a short-term follow-up for the training intervention and a baseline for the later demand experiment. The demand shock occurred in 2022, and a longer-term survey was conducted in 2025. This sequence is useful because it preserves information about firms’ starting readiness before the demand intervention and allows the researchers to look for persistence. It also means the later sample is not simply the original sample observed at regular intervals; eligibility, response, and the changing calendar matter.
The researchers report balanced attrition between treatment and control groups in the follow-up surveys, which supports the basic comparisons. The demand endline analysis nonetheless has changing sample sizes and some baseline imbalances in individual variables. Those facts do not cancel random assignment, but they are reasons to treat subgroup and long-run estimates with care. The study also had difficulty collecting direct revenue information: more than 60% of firms refused to report revenue in the 2025 round. Digital engagement and online selling are consequently more defensible outcomes here than a precise estimate of how much additional income the interventions generated.
What the design lets us ask
The architecture supports a sequence of increasingly specific questions. First, does offering practical digital training change engagement among interested firms? Second, does a concrete conditional buyer change the probability that eligible firms can sell online? Third, does making the prospective order six times larger produce a much bigger response? Fourth, does previous training make firms more responsive to the buyer? Finally, does any early change remain after the special opportunity has passed?
Each question has a different comparison and a different risk of overinterpretation. The training comparison is informative about the effect of assignment to a particular capability-building offer, not the effect of perfect attendance or all possible training. The demand comparison is informative about a time-bound order opportunity in firms selected for current operation and availability, not an unconditional promise that incentives work everywhere. The dose comparison bears on financial sensitivity, but similar responses do not identify one unique psychological mechanism. The overlap comparison bears on complementarity, but its timing and limited size make a precise zero too strong. The endline comparison bears on persistence and catch-up, but its outcome definition and sample differ from the short-run test.
That discipline is more than statistical caution. It keeps the study’s central subject in view. The question is how Georgian small firms move from being able to connect to being able to sell, and what prevents that movement from becoming ordinary business practice. The experiments do not ask whether digital technology is valuable in the abstract. They ask which change in the firm’s circumstances—lowering the presumed cost, supplying a buyer, increasing the return, or combining interventions—actually changes the firm’s behavior.
With that map in place, the first result can be read on its own terms. The training offer was designed to reduce the effort and uncertainty of going online. If firms still did not adopt, the result would weaken the idea that broad technical instruction was the missing piece for this group. It would not close the inquiry, because a firm can know how to act and still lack a reason, deadline, or capacity to do so. The next comparison examines precisely that possibility.