What the Evidence Says About WFH and Moving
First, decide what counts as a move
This chapter examines the evidence that full-time work from home changes migration, with special attention to what the U.S. data can actually measure. That matters because “remote work” and “moving” are broad everyday phrases, while the estimates concern narrower groups, geographic boundaries, and time windows. Readers should come away able to tell a descriptive relationship from stronger—but still conditional—evidence that gaining WFH access raises the chance of moving.
The main U.S. source is the American Community Survey, or ACS. It asks where a person lives now and where they lived one year earlier. A difference between those addresses counts as a residential move. The Dallas Fed study focuses on a move across metropolitan statistical areas, or MSAs. An MSA is a geographic approximation of a labor market: a cluster of communities linked by employment and commuting. Crossing an MSA boundary is therefore more consequential for the job–residence relationship than moving to a different neighborhood within the same labor market. The study also checks interstate migration, but its central results use inter-MSA moves.
The WFH measure is equally specific. In the ACS, a worker is counted as working from home when “worked from home” is the reported usual way of getting to work in the reference week. The measure is designed to capture primarily or fully remote workers. Someone who worked from home one day and commuted on four days is not counted as a full-time WFH worker in this comparison. That makes the estimate useful for studying whether a job can be carried across labor markets, but it limits how far the conclusion can be extended to hybrid workers.
The first pattern is striking even before the pandemic. Between 2015 and 2019, the annual inter-MSA migration rate averaged 2.67% among commuters and 3.78% among WFH workers. The difference—1.11 percentage points—means the WFH rate was about 42% higher relative to the commuter rate. After 2020, the gap did not disappear; on the paper’s measure it widened on average in 2021–24. That persistence is important. If remote workers had moved more only because the pandemic temporarily made some places unattractive, the pre-Covid difference would be harder to explain.
But a persistent difference is not automatically a causal effect. People who work remotely may differ from commuters in ways that also make moving easier or more attractive. They may have different occupations, education, incomes, family situations, preferences, or access to flexible employers. The study therefore estimates the relationship while controlling for observable characteristics such as age, education, income, occupation, industry, marital status, children, and state of residence. The WFH–commuter gap remains visible, especially before 2020. Controls reduce some uncertainty, but they cannot account for preferences or resources that the survey does not observe. They also do not turn a worker’s occupation into a treatment randomly assigned by nature. A high-income employee in a flexible occupation may be more able to pay for a move, more willing to change homes, and more likely to receive remote permission. Those characteristics can travel together. The value of the controlled comparison is therefore not that it removes every alternative explanation. It shows that the WFH label contains information about migration beyond the listed demographic and labor-market characteristics, while leaving unmeasured selection as an open possibility.
The distinction becomes especially important when the paper compares annual rates with the RPS measure since February 2020. An annual ACS rate asks whether a move happened during one particular twelve-month window. The RPS asks whether a respondent has moved at any point since the beginning of the pandemic. The latter can include several years of accumulated decisions and can be higher simply because its window is longer. It is still useful for comparing work-mode transitions, but the percentages should not be placed side by side as if they were the same probability. A sound interpretation keeps the denominator and observation window attached to every estimate.
The geography of the measure also sets a useful boundary. A person who moves from one suburb to another may be responding to rent, space, schools, or amenities without changing employers or labor markets. A person who moves to another MSA may be using remote work to keep an existing job while changing the place where they live. Both are residential moves, but they test different mechanisms. The U.S. result is principally about long-distance movement across labor markets, not about every adjustment a household makes to its home.
When a worker switches into WFH
A snapshot compares different people. A transition comparison asks a more demanding question: among people who commuted before Covid, did those who later switched to full-time WFH move more than those who continued commuting? The Real-Time Population Survey, or RPS, makes this comparison possible. It asks about current work arrangements and asks respondents to recall their work mode in February 2020, just before the pandemic expansion of WFH.
The study divides workers into four conceptual groups. Some commuted both before and after the pandemic. Some worked from home in both periods. Some moved from commuting into WFH. A small group moved in the opposite direction, from WFH into commuting, but it is too imprecise to carry much of the central comparison. The useful contrast is between pre-pandemic commuters who stayed commuters and pre-pandemic commuters who gained access to WFH.
Since February 2020, 5.1% of the commute–commute group had moved MSAs. The corresponding share was 8.6% among commuters who switched to WFH. Workers who WFH in both periods had a similar 8.8% rate. Adding demographic and industry controls changes the comparison little. The pattern fits the portability explanation: once a worker can stay employed while moving, relocation no longer requires giving up the current job at the same moment.
Even this comparison leaves a question about direction of causality. Perhaps people who already wanted to move were more likely to ask their employers for remote permission. In that story, the impending move causes the WFH transition, rather than WFH causing the move. The study addresses this possibility with information about employer policy. It identifies whether a worker’s pre-Covid job could have been done from home and whether the employer changed a WFH policy in a way that affected the worker and co-workers.
The logic is similar to looking for a change that comes from the workplace rather than from a worker’s private relocation plan. A job may have been remote-capable, but the employer required commuting before Covid. Later, the employer may change its policy for a group of employees. If these policy changes strongly predict a switch into WFH and also predict migration, they provide evidence for the idea that access to WFH itself matters. They do not need to predict every worker’s move perfectly; they need to supply variation in WFH access that is plausibly separate from an individual desire to relocate.
In ordinary regressions, switching into WFH increases the predicted probability of an inter-MSA move by roughly 3.3 to 4.2 percentage points. When the policy and job-capacity variables are used as instruments, the estimated effect is larger, ranging across specifications from about 7.1 to 9.3 percentage points. The first-stage tests are strong in the reported specifications, meaning the instruments do predict the WFH switch. The authors interpret the second-stage result as evidence that access to WFH causally increases an individual’s propensity to migrate.
That interpretation is stronger than the original cross-sectional comparison, but it is not the same as a randomized experiment. It relies on an exclusion assumption: after accounting for the included controls, a policy change affecting the worker and co-workers should not be strongly related to that worker’s private wish to move except through WFH access. The RPS is also an online panel rather than a probability sample. The researchers use weights and compare broad patterns with other data, but sampling, retrospective recall, and the restriction to workers with the relevant employment history remain meaningful boundaries.
The transition evidence supports a channel, not a universal rule. It does not say that every hybrid worker will move, that every remote-capable job will remain portable, or that WFH caused every post-pandemic relocation. It says something more precise: when workers who had been commuting gain access to full-time WFH, their measured probability of making a long-distance move rises in a design intended to separate access from individual relocation plans.
From individual transitions to an aggregate increase
The worker-level result has a simple aggregate implication. If WFH workers are more mobile than commuters, then increasing the share of workers in the WFH group can raise the overall migration rate even if neither group changes its own behavior. This is a composition effect. It is like changing the mixture of two populations with different rates: the total can move because the weights change.
The ACS shows the relevant shift. The WFH share rose gradually before Covid, then increased sharply in 2021 and remained well above its pre-pandemic level through 2024. Overall inter-MSA migration also rose above its 2019 rate in the 2021–24 period. To assess how much the changing mixture could account for, the study constructs counterfactual totals. One holds the commuter and WFH shares at their 2019 levels while allowing the group-specific migration rates to vary. Another holds both the 2019 group shares and the 2019 WFH migration rate fixed.
The difference between actual migration and the first counterfactual attributes a sizable share of the increase to the larger WFH group. On average, the paper reports that the higher WFH share statistically accounts for 53% of the increase relative to 2019. Including both the larger WFH share and the higher migration rate of WFH workers raises the accounted-for share to 64%.
These numbers are useful because they quantify a channel that a headline total hides. They also require careful wording. The calculation holds selected shares and rates fixed; it does not recreate the entire economy with and without WFH. It does not rule out other forces that changed at the same time, such as housing demand, health concerns, immigration, local crime, or changing preferences about density. “Accounts for” here means that the observed change is statistically allocated by a transparent counterfactual, not that a complete causal decomposition has been established.
The distinction between composition and behavior also matters for the broader theme. The aggregate increase does not require every WFH worker to become dramatically more mobile. A relatively small group with a persistently higher migration rate can have a large effect when its share expands. That is why the question “who can leave?” is more informative than a citywide average. The change in the composition of workers determines whose choices are being counted more heavily.
The counterfactual is also a reminder that attribution depends on the comparison being made. Holding the WFH share at its earlier level asks what migration would have looked like if the population mix had not changed, while allowing the observed commuter and WFH rates to continue. Holding both the share and the WFH rate fixed asks a still different question: what if neither the composition nor the unusually high mobility of WFH workers had changed? The gap between these counterfactuals is not a policy estimate and does not describe a world in which the pandemic never happened. It is a way to separate two arithmetic channels inside the observed data. A city planner can use that separation to ask better questions, but cannot read it as a complete forecast of what a city would have experienced under a different work regime.
The evidence has now established two linked but different claims. First, WFH workers moved across MSAs at higher rates than commuters, even before the pandemic, and observable controls do not erase the gap. Second, workers who switched into WFH moved more than comparable workers who continued commuting, and employer-policy variation supports a causal interpretation of the access channel. Third, the larger WFH population can explain a substantial portion of the aggregate migration increase through composition, but the accounting is not a complete explanation of every move.
Those qualifications are not a retreat from the result. They tell us what the result is. It is evidence that loosening the job–residence tie changes mobility, strongest when we compare a work transition and preserve the instrument’s assumptions. It is not evidence that all residents respond alike, that all remote work is full-time, or that a national migration statistic reveals the same mechanism as a local residential move. The next question is therefore geographical: once workers have more ability to move, which places become their destinations and what trade-offs do those choices reveal?