the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 10 Mar 2026
The impact of the Canterbury earthquakes on household income and expenditure in the Canterbury region in New Zealand
Abstract. Using New Zealand's Integrated Data Infrastructure (IDI), we evaluate the impact of the 2010–2011 Canterbury earthquakes on household economic behaviour, focusing on changes in income and expenditure. Using nationally representative data from the Household Economic Survey (HES) linked to measures of earthquake intensity, we implement a difference-in-differences design comparing pre- and post-earthquake outcomes for earthquake-affected households with a matched comparison group. We find that, relative to matched comparison households, total household income in high-intensity areas increases by about NZD 7,600 in the post-earthquake period. Total expenditure shows no clear average DiD effect, but expenditure composition shifts markedly: receipts and refunds, which capture insurance reimbursements and related inflows, more than double, and diary-recorded day-to-day spending rises by about 14 %. Spending also increases in transportation, travel, fees and subscriptions, and social insurance contributions. Additional analysis shows that households that relocated out of Canterbury faced substantially higher housing costs (around NZD 25,000) and lower mortgage and loan repayments (around NZD 9,500) than households that remained, while average incomes are similar across the two groups. These findings provide evidence on household economic adjustment to disasters and offer policy-relevant insights into post-disaster financial support, social security design, and the management of population movements.
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Status: open (until 21 Apr 2026)
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RC1: 'Comment on egusphere-2026-1005', Anonymous Referee #1, 13 Mar 2026
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AC1: 'Reply on RC1', Quanfu Zhang, 11 Apr 2026
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We thank Referee #1 for the careful reading of our paper and for the constructive comments. We appreciate the referee’s positive assessment of the paper as competent and useful, and we are grateful for the two specific suggestions. Below we respond to each point in turn.
Comment 1: “Please add a specification with the MMI, rather than its discretization into three classes (zero, low, high).”
Our reason for using grouped intensity categories rather than a continuous MMI specification is that, in our setting, the household economic response to earthquake intensity is unlikely to be well captured by a simple linear dose-response relationship. We are interested in whether households exposed to meaningfully different levels of earthquake intensity exhibit different post-earthquake economic adjustments, and this is naturally consistent with a threshold-based or regime-based interpretation rather than a strictly linear one.
In addition, the categorisation used in the paper is not intended to be ad hoc. The thresholds are informed by the relevant literature and by the substantive interpretation of different levels of earthquake exposure. For this reason, we view the zero/low/high specification as a more interpretable way to capture meaningful exposure heterogeneity in this context.
We will clarify this motivation more explicitly in the revised manuscript, and, if needed, assess the robustness of the results to alternative reasonable threshold definitions.
Comment 2: “Please add a balancing test between waves. You match treatment and control. Are there changes between waves that could endanger identification?”
In our design, propensity score matching is conducted separately within each survey wave, so treated households are compared with contemporaneously matched controls rather than with a single pooled control group. This already helps reduce concerns about between-wave imbalance.
To further assess whether compositional changes across waves could threaten identification, we conducted additional placebo-style balance tests in the matched sample using key observed household characteristics as pseudo-outcomes in a DID framework. Specifically, we estimated the interaction term Treat×Post for the reference person’s age, household size, sex, tenure status, and education, including survey-wave fixed effects.
The estimated interaction coefficients are uniformly small and statistically insignificant. This suggests that the matched treated and control samples do not exhibit systematic differential compositional shifts across waves in these observable characteristics. We will report these results in the revised manuscript to make the identification argument clearer.
Once again, we thank the referee for these helpful comments. We believe they improve the clarity of the paper, especially in explaining our treatment-intensity specification and in strengthening the discussion of balance and identification across survey waves.
Citation: https://doi.org/10.5194/egusphere-2026-1005-AC1
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AC1: 'Reply on RC1', Quanfu Zhang, 11 Apr 2026
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RC2: 'Comment on egusphere-2026-1005', Anonymous Referee #2, 01 Apr 2026
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The authors are working on an important topic with a reasonable approach and a data set that appears to have some very important advantages. Having read many papers in this area, very few can differentiate between earned income, which can be impacted by a disaster, and insurance payouts. Many studies have reported surprisingly little financial hardship around disaster events, and those authors could only speculate that public or private insurance payments smoothed consumption. The disaggregated expenditure data is also uncommon. Considering how extensive the literature on disaster impacts on households is at this point, more of the literature should probably be cited, including papers whose limitations you are overcoming.
I have a few suggestions for improving the analysis or clarifying what was already done.
The authors have linked records, which enables them to do analysis on people who stay in place vs. those who migrate. However, I didn’t understand how persistent the sample is. The observation counts in table A.1 vary by over 66% between high and low years for group 1 and 100% in group 4. Do the people in the lowest year persist all the way through while others come and go? Are there people with all combinations of years observable? For example, could someone be observed only in 2006, 2009 and 2016 and another person observed only in 2010, 2011, and 2012? With the modest sample sizes, it seems like people entering and exiting the sample could have substantial impacts on the estimates and precision. If this is more like a repeated cross section than a balanced individual panel, you would need to approach it with different methods.
I was puzzled by the use of covariates in the specification. As the authors discuss in lines 719-729, no one would expect age to have a linear relationship with income or expenditures. Why put it in the model as linear when you could include it in a more flexible and realistic form? Similarly with the household structure. The relationship between household size, income and expenditures will be very different moving from one to two working adults versus adding a third or fourth child. Why not have indicators for a handful of common household types (single working person, dual income no kids, dual income with kids, single income with kids, retirees, etc.)?
The event study graphs in Appendix C do not improve my confidence in the results. It would not be fully transparent to place them in an appendix that most readers wouldn’t see. My concern is that all the pre-treatment coefficients are substantially above zero. The wide confidence intervals include zero, but four of the seven post-event coefficients are at the same levels, as if the earthquake had no impact. The three periods of higher income appear 4 to 7 years after the event. Impacts persisting seven years later is plausible, but if these are driven by insurance payouts and rebuilding, shouldn’t we see something in post-years 1, 2 and 3?
Did the authors try inverse probability weighting to see if it is any better than PSM at reducing the pre-treatment coefficients or improving precision (I apologize if I missed it)? Is there any way of expanding the pool of potential controls, which would increase the quality of the matches and give us more confidence in the results?
Finally, I’ll request a few minor clarifications for readers who have never had the privilege of visiting New Zealand. What are the important differences between the North and South Islands, and why should I be comfortable with the control group being drawn entirely from a different island? Consider replacing “Contribution Schemes” with “Retirement Savings.” I didn’t know what specifically was being contributed to until you mentioned it in the text. I expect all readers would understand “retirement.”
Citation: https://doi.org/10.5194/egusphere-2026-1005-RC2
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This is a competent and useful but modest paper.
I would add two things. First, please add a specification with the MMI, rather than its discretization into three classes (zero, low, high).
Second, please add a balancing test between waves. You match treatment and control. Are there changes between waves that could endanger identification?