Assumes that outcomes change only as a result of exposure to the intervention
Abbreviations: LMIC, low- and middle-income countries; NE, natural experiment.
Standard multivariable models, which control for observed differences between intervention and control groups, can be used to evaluate NEs when no important differences in unmeasured characteristics between intervention and control groups are expected (see Model 1 in Appendix 1 ). Goodman et al. used data from the UK Millennium Cohort Study to evaluate the impact of a school-based cycle training scheme on children’s cycling behavior ( 29 ). The timing of survey fieldwork meant that some interviews took place before and others after the children received training. Poisson models were used to estimate the effect of training on cycling behaviors, with adjustment for a wide range of potential confounders. Previous evaluations that compared children from participating and nonparticipating schools found substantial effects on cycling behavior. In contrast, this study found no difference, suggesting that the earlier findings reflected the selective provision of training. The key strength of the study by Goodman et al. is the way the timing of data gathering in relation to exposure created well-balanced intervention and control groups. Without this overlap between data gathering and exposure to the intervention, there was a significant risk that unobserved differences between the groups would bias the estimates, despite adjusting for a wide range of observed confounders.
In a well-conducted RCT, random allocation ensures that intervention and control arms are balanced in terms of both measured and unmeasured covariates. In the absence of random allocation, the propensity score attempts to recreate the allocation mechanism, defined as the conditional probability of an individual being in the intervention group, given a number of covariates ( 65 ).
The propensity score is typically estimated using logistic regression, based on a large number of covariates, although alternative estimation methods are available. There are four principal ways to use the propensity score to obtain an estimated treatment effect: matching, stratification, inverse probability weighting, and covariate adjustment ( 7 ). Each method will adjust for differences in characteristics of the intervention and control groups and, in so doing, minimize the effects of confounding. The propensity score, however, is constrained by the covariates available and the extent to which they can collectively mimic the allocation to intervention and control groups.
Understanding the mechanism underlying allocation to intervention and control groups is key when deriving the propensity score. Sure Start Local Programmes (SSLPs), area-based interventions designed to improve the health and well-being of young children in England, were an example where, on an ITT basis, exposure to the intervention was determined by area of residence and would apply to everyone living in the area regardless of individual characteristics. Melhuish et al. ( 54 ) therefore constructed a propensity score at the area level, based on 85 variables, to account for differences between areas with and without SSLPs. Analysis was undertaken on individuals clustered within areas, stratified by the propensity of an area to receive the SSLP. The most deprived areas were excluded from the analysis because there were insufficient comparison areas.
Advantages of using the propensity score over simple regression adjustment include the complexity of the propensity score that can be created (through, for example, including higher-order terms and interactions), the ease of checking the adequacy of the propensity score as opposed to checking the adequacy of a regression model, and the ability to examine the extent to which intervention and control groups overlap in key covariates ( 7 , 18 ), and thereby avoid extrapolation. Although in statistical terms the use of propensity scores may produce results that differ little from those obtained through traditional regression adjustment ( 70 ), they encourage clearer thinking about study design and particularly the assignment mechanism ( 66 ). When membership of the treatment and control groups varies over time, inverse probability weighting can be used to account for time-varying confounding ( 34 ), as in the study by Pega et al. ( 59 ) of the cumulative impact of tax credits on self-rated health.
In its simplest form, the DiD approach compares change in an outcome among people who are newly exposed to an intervention with change among those who remain unexposed. Although these differences could be calculated from a 2 × 2 table of outcomes for each group at each time point, the effect is more usefully estimated from a regression with terms for group, period, and group-by-period interaction. The coefficient of the interaction term is the DiD estimator (Model 2 in Appendix 1 ).
DiD’s strength is that it controls for unobserved as well as observed differences in the fixed (i.e., time-invariant) characteristics of the groups and is therefore less prone to omitted variable bias caused by unmeasured confounders or measurement error. The method relies on the assumption that, in the absence of the intervention, preimplementation trends would continue. This common trends assumption may be violated by differential changes in the composition of the intervention or control groups or by other events (such as the introduction of another intervention) that affect one group but not the other. With data for multiple preimplementation time points, the common trends assumption can be investigated directly, and it can be relaxed by extending the model to include terms for group-specific trends. With more groups and time points, the risk that other factors may influence outcomes increases, but additional terms can be included to take account of time-varying characteristics of the groups.
De Angelo & Hansen ( 19 ) used a DiD approach to estimate the effectiveness of traffic policing in reducing road traffic injuries and fatalities by taking advantage of a NE provided by the state of Oregon’s failure to agree on a budget in 2003, which led to the layoff of more than one-third of Oregon’s traffic police force. A comparison of injury and fatality rates in Oregon with rates in two neighboring states before and after the layoff indicated that, after allowing for other factors associated with road traffic incidents, such as the weather and the number of young drivers, less policing led to a 12–14% increase in fatalities. Whereas De Angelo & Hansen’s study focused on an intervention in a single area, Nandi and colleagues ( 58 ) applied DiD methods to estimate the impact of paid maternity leave across a sample of 20 low- and middle-income countries.
DiD methods are not limited to area-based interventions. Dusheiko et al. ( 23 ) used the withdrawal of a financial incentive scheme for family doctors in the English National Health Service to identify whether it led to treatment rationing. Recent developments, such as the use of propensity scores, rather than traditional covariate adjustment, to account for group-specific time-varying characteristics, add additional complexity, but combining DiD with other approaches in this way may further strengthen causal inference.
Alongside DiD, ITS methods are among the most widely applied approaches to evaluating NEs. An ITS consists of a sequence of count or continuous data at evenly spaced intervals over time, with one or more well-defined change points that correspond to the introduction of an intervention ( 69 ). There are many approaches to analyzing time series data ( 44 ). A straightforward approach is to use a segmented regression model, which provides an estimate of changes in the level and trend of the outcome associated with the intervention, controlling for preintervention level and trend ( 43 , 75 ). Such models can be estimated by fitting a linear regression model, including a continuous variable for time since the start of the observation period, a dummy variable for time period (i.e., before/after intervention), and a continuous variable for time postintervention (Model 3 in Appendix 1 ). The coefficients of these variables measure the preintervention trend, the change in the level of the outcome immediately postintervention, and the change in the trend postintervention. Additional variables can be added to identify the effects of interventions introduced at other time points or to control for changes in level or trend of the outcome due to other factors. Lags in the effect of the intervention can be accounted for by omitting outcome values that occur during the lag period or by modeling the lag period as a separate segment ( 75 ). Successive observations in a time series are often related to one another, a problem known as serial autocorrelation. Unless autocorrelation is addressed, the standard errors will be underestimated, but models that allow for autocorrelation can be fitted using standard statistical packages.
By accounting for preintervention trends, well-conducted ITS studies permit stronger causal inference than do cross-sectional or simple prepost designs, but they may be subject to confounding by cointerventions or changes in population composition. Controlled ITS designs, which compare trends in exposed and unexposed groups or in outcomes that are not expected to change as a result of the intervention, can be used to strengthen causal inference still further; in addition, standardization can be used to control for changes in population composition. A common shortcoming in ITS analyses is a lack of statistical power ( 61 ). Researchers have published a range of recommendations for the number of data points required, but statistical power also depends on the expected effect size and the degree of autocorrelation. Studies with few data points will be underpowered unless the effect size is large. Zhang et al. ( 79 ) and Mcleod & Vingilis ( 53 ) provide methods for calculating statistical power for ITS studies.
Robinson et al. ( 64 ) applied controlled ITS methods to commercially available alcohol sales data to estimate the impact of a ban on the offer of multipurchase discounts by retailers in Scotland. Because alcohol sales vary seasonally, the researchers fitted models that took account of seasonal autocorrelation, as well as trends in sales in England and Wales where the legislation did not apply. After adjusting for sales in England and Wales, the study found a 2% decrease in overall sales, compared with a previous study’s finding of no impact using DiD methods applied to self-reported alcohol purchase data.
The difficulty of finding control areas that closely match the background trends and characteristics of the intervention area is a significant challenge in many NE studies. One solution is to use a synthetic combination of areas rather than the areas themselves as controls. Methods for deriving synthetic controls and using them to estimate the impact of state-, region-, or national-level policies were developed by political scientists ( 1 – 4 ) and are now being applied to many health and social policies ( 8 , 9 , 17 , 30 , 45 , 62 , 67 ).
A synthetic control is a weighted average of control areas that provides the best visual and statistical match to the intervention area on the preintervention values of the outcome variable and of predictors of the outcome. Although the weights are based on observed characteristics, matching on the outcome in the preintervention period minimizes differences in unobserved fixed and time-varying characteristics. The difference between the postintervention trend in the intervention and synthetic control provides the effect estimate. Software to implement the method is available in a number of statistical packages ( 2 ).
Abadie et al. ( 1 ) used synthetic controls to evaluate a tobacco control program introduced in California in 1988, which increased tobacco taxes and earmarked the revenues for other tobacco control measures. The comparator was derived from a donor pool of other US states, excluding any states that had implemented extensive tobacco control interventions. A weighted combination of five states, based on pre-1988 trends in cigarette consumption and potential confounders, formed the synthetic control. Comparison of the postintervention trends in the real and synthetic California suggested a marked reduction in tobacco consumption as a result of the program.
The synthetic control method can be seen as an extension of the DiD method, with a number of advantages. In particular, it relaxes the requirement for a geographical control that satisfies the parallel trends assumption and relies less on subjective choices of control areas. A practical limitation, albeit one that prevents extrapolation, is that if the intervention area is an outlier, for example if California’s smoking rate in 1988 was higher than those of all other US states, then no combination of areas in the donor pool can provide an adequate match. Another limitation is that conventional methods of statistical inference cannot be applied, although Abadie et al. ( 1 ) suggest an alternative that compares the estimated effect for the intervention area with the distribution of placebo effects derived by comparing each area in the donor pool with its own synthetic control.
IV methods address selective exposure to an intervention by replacing a confounded direct measure of exposure with an unconfounded proxy measure, akin to treatment assignment in an RCT ( 33 ). To work in this way, an IV must be associated with exposure to the intervention, must have no association with any other factors associated with exposure, and must be associated with outcomes only through its association with exposure to the intervention ( Figure 1 ).
( a ) The variable Z is associated with outcome Y only through its association with exposure X , so it can be considered a valid instrument of X . ( b ) Z is not a valid instrument owing to a lack of any association with outcome Y . ( c ) Z is not a valid instrument owing to its association with confounder C . ( d ) Z is not a valid instrument owing to its direct association with Y .
IVs that satisfy the three conditions offer a potentially valuable solution to the problem of unobserved as well as observed confounders. Estimating an intervention’s effect using IVs can be viewed as a two-stage process (Models 5.1 and 5.2 in Appendix 1 ). In the first stage, a prediction of treatment assignment is obtained from a regression of the treatment variable on the instruments. Fitted values from this model replace the treatment variable in the outcome regression ( 41 ).
IVs are widely used in econometric program evaluation and have attracted much recent interest in epidemiology, particularly in the context of Mendelian randomization studies, which use genetic variants as instruments for environmental exposures ( 25 , 36 , 48 ). IV methods have not yet been widely used to evaluate public health interventions because it can be difficult to find suitable instruments and to demonstrate convincingly, using theory or data, that they meet the second and third conditions above ( 35 , 71 ). A recent example is the study by Ichida et al. ( 39 ) of the effect of community centers on improving social participation among older people in Japan, using distance to the nearest center as an instrument for intervention receipt. Another study, by Yen et al. ( 78 ), considers the effect of food stamps on food insecurity, using a range of instruments, including aspects of program administration that might encourage or discourage participation in the food stamp program. Given the potential value of IVs, as one of a limited range of approaches for mitigating the problems associated with unobserved confounders, and their widespread use in related fields, they should be kept in mind should opportunities arise ( 35 ).
Age, income, and other continuous variables are often used to determine entitlement to social programs, such as means-tested welfare benefits. The RD design uses such assignment rules to estimate program impacts. RD is based on the insight that units with values of the assignment variable just above or below the cutoff for entitlement will be similar in other respects, especially if there is random error in the assignment variable ( 11 ). This similarity allows the effect of the program to be estimated from a regression of the outcome on the assignment variable (often referred to as the running or forcing variable) and a dummy variable denoting exposure (treatment), with the coefficient of the dummy identifying the treatment effect (Model 4 in Appendix 1 ). Additional terms are usually included in the model to allow slopes to vary above and below the cutoff, allow for nonlinearities in the relationship between the assignment and outcome variables, and deal with residual confounding.
Visual checks play an important role in RD studies. Plots of treatment probability ( Figure 2 ) and outcomes against the assignment variable can be used to identify discontinuities that indicate a treatment effect, and a histogram of the assignment variable can be plotted to identify bunching around the cutoff that would indicate manipulation of treatment assignment. Scatterplots of covariates against assignment can be used to check for continuity at the cutoff that would indicate whether units above and below the cutoff are indeed similar ( 57 ).
( a ) A fuzzy regression discontinuity: probability of treatment changes gradually at values of the assignment variable close to the cutoff. ( b ) A sharp regression discontinuity: probability of treatment changes from 0 to 1 at the cutoff. Source: Reproduced from Moscoe (2015) ( 57 ) with permission from Elsevier.
The RD estimator need not be interpreted only as the effect of a unit’s exposure to the program (treatment) right at the cutoff value ( 47 ), but the assumption that units above and below the cutoff are similar except in their exposure to the program becomes less tenable as distance from the cutoff increases. Usual practice is to fit local linear regressions for observations within a narrow band on either side of the cutoff. Restricting the analysis in this way also means that nonlinearities in the relationship between the forcing and outcome variables are less important. One drawback is that smaller numbers of observations will yield less precise estimates, so the choice involves a trade-off between bias and precision.
The above approach works when the probability of a treatment jumps from 0 to 1 at the cutoff, which is known as sharp RD ( Figure 2b ). If exposure is influenced by factors other than the value of the forcing variable, for example because administrators can exercise discretion over whom to include in the program or because individuals can, to some extent, manipulate their own assignment, the probability of treatment may take intermediate values close to the cutoff ( Figure 1b ) and a modified approach known as fuzzy RD should be applied. This process uses the same two-stage approach to estimation as does an IV analysis (Models 5.1 and 5.2 in Appendix 1 ).
One example of a sharp RD design is Ludwig & Miller’s ( 52 ) analysis of the US Head Start program. Help with applications for Head Start funding was targeted to counties with poverty rates of 59% or greater. This targeting led to a lasting imbalance in the receipt of Head Start funds among counties with poverty rates above and below the cutoff. Ludwig & Miller used local linear regressions of mortality on poverty rates for counties with poverty rates between 49% and 69%; the impact of the Head Start funding was defined as the difference between the estimated mortality rates at the upper and lower limits of this range. They found substantial reductions in mortality from causes amenable to Head Start but not from other causes of death or in children whose ages meant they were unlikely to benefit from the program.
Andalon ( 6 ) used a fuzzy RD design to investigate the impact of a conditional cash transfer program on obesity and overweight. Mexico’s Opportunidades program provided substantial cash subsidies to households in rural communities that scored below a poverty threshold, which were conditional on school and health clinic attendance. There were a range of other ad hoc adjustments to eligibility criteria, creating a fuzzy rather than a sharp discontinuity in participation at the poverty cutoff. Andalon used two-stage least squares regression to estimate the effect of eligibility (based on the poverty score) on program participation and the effect of predicted participation on obesity and overweight. The author found no effect for men but a substantial reduction in obesity among women. Further testing indicated no bunching of poverty scores around the cutoff and no significant discontinuity at the cutoff in a range of covariates. Inclusion of the covariates in the outcome regressions had little effect on the estimates, further supporting the assumption of local randomization.
RD methods are widely regarded as the closest approximation of an observational study to an RCT ( 5 ), but their real value derives from their wide applicability to the evaluation of social programs for which eligibility is determined by a score on some form of continuous scale and also from their reliance on relatively weak, directly testable assumptions. One key shortcoming is that restricting the bandwidth to reduce bias results in a loss of precision ( 46 , 73 ), and estimates that may hold over only a small segment of the whole population exposed to the intervention. This restriction to a subset of the population may not matter if the intervention is expected to affect outcomes locally, as in the case of a minimum legal drinking age or if the substantive focus of the study is on the effect of a small change in the assignment rule. It is more serious when the outcome of interest is the effect on the whole population.
Causal inference can be strengthened in NE studies by the inclusion of additional design features alongside the principal method of effect estimation. Studies should be based on a clear theoretical understanding of how the intervention achieves its effects and the processes that determine exposure. Even if the observed effects are large and rapidly follow implementation, confidence in attributing them to the intervention can be markedly improved by a detailed consideration of alternative explanations.
Qualitative research can strengthen the design of RCTs of complex public health interventions ( 10 , 56 ), and this argument applies equally to NEs ( 38 ). Qualitative research undertaken in preparation for, or alongside, NE studies can help to identify which outcomes might change as a consequence of the intervention and which are priorities for decision makers ( 42 ). It can also improve understanding of the processes that determine exposure, factors associated with intervention delivery and compliance, mechanisms by which outcomes are realized, and the strengths and limitations of routinely collected measures of exposures and outcomes ( 13 ). Qualitative studies conducted alongside the quantitative evaluation of Scotland’s smoke-free legislation have been used to assess compliance with the intervention ( 24 ) and to identify a range of secondary outcomes such as changes in smoking behavior within the home ( 60 ). Qualitative methods for identifying the effects of interventions have also been proposed, but further studies are needed to establish their validity and usefulness ( 63 , 72 , 77 ).
Quantitative methods for strengthening inference include the use of multiple estimation methods within studies, replication studies, and falsification tests. Tests specific to particular methods, such as visual checks for discontinuities in RD and ITS studies, can also be used. Good-quality NE studies typically use a range of approaches. Comparing results obtained using different methods can be used to assess the dependence of findings on particular assumptions ( 50 ). Such comparisons are particularly useful in early applications of novel methods whose strengths and weaknesses are not fully understood ( 49 ).
Falsification or placebo tests assess the plausibility of causal attribution by checking for the specificity of effects. One such approach is to use nonequivalent dependent variables to measure changes in outcomes that are not expected to respond to the intervention. They serve as indicators of residual confounding or the effects of other interventions introduced alongside the study intervention. A related approach is to use false implementation dates and to compare changes associated with those dates with effects estimated for the real implementation date. A similar test used in synthetic control studies involves generating placebo effects by replacing the intervention area with each of the areas in the donor pool in turn and then comparing the estimated intervention effect with the distribution of placebo effects ( 1 , 2 ).
Most NE studies are conducted retrospectively, using data collected before the study is planned. Ideally, an analysis protocol, setting out hypotheses and methods, should be developed before any data analysis is conducted ( 21 ). Even when such protocols are published, they do not provide a perfect safeguard against selective reporting of positive findings. Replication studies, which by definition retest a previously published hypothesis, are a valuable additional safeguard against retrospectively fitting hypotheses to known features of the data. Reporting of NE studies of all kinds may also be improved by following established reporting guidelines such as STROBE (Strengthening the Reporting of Observational Studies in Epidemiology) ( 74 ) or TREND (Transparent Reporting of Evaluations with Nonrandomized Designs) ( 28 ).
NE approaches to evaluation have become topical because they address researchers’ and policy makers’ interests in understanding the impact of large-scale population health interventions that, for practical, ethical, or political reasons, cannot be manipulated experimentally. We have suggested a pragmatic approach to NEs. NEs are not the answer to every evaluation question, and it is not always possible to conduct a good NE study whenever an RCT would be impractical. Choices among evaluation approaches are best made according to specific features of the intervention in question, such as the allocation process, the size of the population exposed, the availability of suitable comparators, and the nature of the expected impacts, rather than on the basis of general rules about which methods are strongest, regardless of circumstances. Availability of data also constrains the choice of methods. Where data allow, combining methods and comparing results are good ways to avoid overdependence on particular assumptions. Having a clear theory of change based on a sound qualitative understanding of the causal mechanisms at work is just as important as sophisticated analytical methods.
Many of the examples discussed above use routinely collected data on outcomes such as mortality, road traffic accidents, and hospital admissions and data on exposures such as poverty rates, alcohol sales, and tobacco consumption. Continued investment in such data sources, and in population health surveys, is essential if the potential for NEs to contribute to the evidence base for policy making is to be realized. Recent investments in infrastructure to link data across policy sectors for research purposes are a welcome move that should increase opportunities to evaluate NEs ( 12 , 26 , 37 ). Funding calls for population health research proposals should take a similarly even-handed approach to specifying which approaches would be acceptable and should emphasize the importance of developing a clear theory of change, carefully testing assumptions, and comparing estimates from alternative methods.
Acknowledgments.
The authors receive core funding from the UK Medical Research Council (funding codes: MC_UU_12017/13, MC_UU_12017/15) and the Scottish Government Chief Scientist Office (funding codes: SPHSU13 and SPHSU15). In addition, S.V.K. is funded by an NHS Research Scotland Senior Clinical Fellowship (SCAF/15/02). The funders had no role in the preparation or submission of the manuscript, and the views expressed are those of the authors alone.
Disclosure Statement
The authors are not aware of any affiliations, memberships, funding, or financial holdings that might be perceived as affecting the objectivity of this review.
Volume 38, 2017, review article, open access, natural experiments: an overview of methods, approaches, and contributions to public health intervention research.
Population health interventions are essential to reduce health inequalities and tackle other public health priorities, but they are not always amenable to experimental manipulation. Natural experiment (NE) approaches are attracting growing interest as a way of providing evidence in such circumstances. One key challenge in evaluating NEs is selective exposure to the intervention. Studies should be based on a clear theoretical understanding of the processes that determine exposure. Even if the observed effects are large and rapidly follow implementation, confidence in attributing these effects to the intervention can be improved by carefully considering alternative explanations. Causal inference can be strengthened by including additional design features alongside the principal method of effect estimation. NE studies often rely on existing (including routinely collected) data. Investment in such data sources and the infrastructure for linking exposure and outcome data is essential if the potential for such studies to inform decision making is to be realized.
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Natural experiments as quasi experiments, instrumental variables.
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natural experiment , observational study in which an event or a situation that allows for the random or seemingly random assignment of study subjects to different groups is exploited to answer a particular question. Natural experiments are often used to study situations in which controlled experimentation is not possible, such as when an exposure of interest cannot be practically or ethically assigned to research subjects. Situations that may create appropriate circumstances for a natural experiment include policy changes, weather events, and natural disasters. Natural experiments are used most commonly in the fields of epidemiology , political science , psychology , and social science .
Key features of experimental study design include manipulation and control. Manipulation, in this context , means that the experimenter can control which research subjects receive which exposures. For instance, subjects randomized to the treatment arm of an experiment typically receive treatment with the drug or therapy that is the focus of the experiment, while those in the control group receive no treatment or a different treatment. Control is most readily accomplished through random assignment, which means that the procedures by which participants are assigned to a treatment and control condition ensure that each has equal probability of assignment to either group. Random assignment ensures that individual characteristics or experiences that might confound the treatment results are, on average, evenly distributed between the two groups. In this way, at least one variable can be manipulated, and units are randomly assigned to the different levels or categories of the manipulated variables.
In epidemiology, the gold standard in research design generally is considered to be the randomized control trial (RCT). RCTs, however, can answer only certain types of epidemiologic questions, and they are not useful in the investigation of questions for which random assignment is either impracticable or unethical. The bulk of epidemiologic research relies on observational data, which raises issues in drawing causal inferences from the results. A core assumption for drawing causal inference is that the average outcome of the group exposed to one treatment regimen represents the average outcome the other group would have had if they had been exposed to the same treatment regimen. If treatment is not randomly assigned, as in the case of observational studies, the assumption that the two groups are exchangeable (on both known and unknown confounders) cannot be assumed to be true.
As an example, suppose that an investigator is interested in the effect of poor housing on health. Because it is neither practical nor ethical to randomize people to variable housing conditions, this subject is difficult to study using an experimental approach. However, if a housing policy change, such as a lottery for subsidized mortgages, was enacted that enabled some people to move to more desirable housing while leaving other similar people in their previous substandard housing, it might be possible to use that policy change to study the effect of housing change on health outcomes. In another example, a well-known natural experiment in Helena , Montana, smoking was banned from all public places for a six-month period. Investigators later reported a 60-percent drop in heart attacks for the study area during the time the ban was in effect.
Because natural experiments do not randomize participants into exposure groups, the assumptions and analytical techniques customarily applied to experimental designs are not valid for them. Rather, natural experiments are quasi experiments and must be thought about and analyzed as such. The lack of random assignment means multiple threats to causal inference , including attrition , history, testing, regression , instrumentation, and maturation, may influence observed study outcomes. For this reason, natural experiments will never unequivocally determine causation in a given situation. Nevertheless, they are a useful method for researchers, and if used with care they can provide additional data that may help with a research question and that may not be obtainable in any other way.
The major limitation in inferring causation from natural experiments is the presence of unmeasured confounding. One class of methods designed to control confounding and measurement error is based on instrumental variables (IV). While useful in a variety of applications, the validity and interpretation of IV estimates depend on strong assumptions, the plausibility of which must be considered with regard to the causal relation in question.
In particular, IV analyses depend on the assumption that subjects were effectively randomized, even if the randomization was accidental (in the case of an administrative policy change or exposure to a natural disaster) and adherence to random assignment was low. IV methods can be used to control for confounding in observational studies, to control for confounding due to noncompliance, and to correct for misclassification.
IV analysis, however, can produce serious biases in effect estimates. It can also be difficult to identify the particular subpopulation to which the causal effect IV estimate applies. Moreover, IV analysis can add considerable imprecision to causal effect estimates. Small sample size poses an additional challenge in applying IV methods.
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Background: Natural or quasi experiments are appealing for public health research because they enable the evaluation of events or interventions that are difficult or impossible to manipulate experimentally, such as many policy and health system reforms. However, there remains ambiguity in the literature about their definition and how they differ from randomized controlled experiments and from other observational designs. We conceptualise natural experiments in the context of public health evaluations and align the study design to the Target Trial Framework.
Methods: A literature search was conducted, and key methodological papers were used to develop this work. Peer-reviewed papers were supplemented by grey literature.
Results: Natural experiment studies (NES) combine features of experiments and non-experiments. They differ from planned experiments, such as randomized controlled trials, in that exposure allocation is not controlled by researchers. They differ from other observational designs in that they evaluate the impact of events or process that leads to differences in exposure. As a result they are, in theory, less susceptible to bias than other observational study designs. Importantly, causal inference relies heavily on the assumption that exposure allocation can be considered 'as-if randomized'. The target trial framework provides a systematic basis for evaluating this assumption and the other design elements that underpin the causal claims that can be made from NES.
Conclusions: NES should be considered a type of study design rather than a set of tools for analyses of non-randomized interventions. Alignment of NES to the Target Trial framework will clarify the strength of evidence underpinning claims about the effectiveness of public health interventions.
Keywords: Evaluations; Natural experiments; Public health; Public health policy; Quasi experiments.
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Natural Experiments
You have just learned that it is hard to infer causality from an observational study. With observational studies, it is usually much harder to control for confounding variables. However, researchers have come up with ways to control for confounding variables even when treatment assignment is not under the control of the researcher. One example of this is a research design called the natural experiment.
We have a natural experiment when variation in the independent variable is randomly assigned, but not by the researcher. One example of a natural experiment was conducted in Brazil: researchers wanted to know if voters punish politicians when they discover that politicians are involved in corruption.
The researchers noticed that the federal government of Brazil conducted audits to find out whether or not the mayors of local towns are involved in corruption. The federal government did not have the capacity to conduct such audits in every single town, so they had to choose a group of towns to be audited.
To avoid suspicion that the audits were used to persecute opponents, the government decided that the group of towns to be audited would be randomly selected. This gave researchers an opportunity to test the following question: what happens to the reelection chances of mayors who get audited, when compared to mayors who do not get audited?
They found that, when compared to mayors who do not get audited, honest mayors who were audited and came clean were more likely to be reelected. By contrast, corrupt mayors who were audited and got caught were less likely to be reelected than mayors who were not audited. We know that these outcomes were caused by the audits because audits were randomly assigned. Because of random assignment, the researchers were able to rule out confounding variables: towns that were audited are similar, on average, to towns that were not audited.
When a researcher notices that variation in an independent variable is random, and uses this random assignment to draw causal inference, we see an example of a natural experiment. The researchers exploited the fact that the Brazilian government randomly assigned variation in which towns get audited--the independent variable of interest.
Quasi-Experiments
A quasi-experiment is an experiment that looks like a true, randomized experiment, but lacks random assignment. One example of a quasi-experiment is when treatment is not randomly assigned, but we have reasons to believe that the treatment group is similar to the control group.
For example, think about a high school that wants to measure the impact of the Covid pandemic on student performance. At this school, the class of 2019 suffered no impact from the pandemic, the class of 2020 suffered some impact, and the class of 2021 suffered a lot of impact. So long as we believe that students in the classes of 19, 20 and 21 are similar to each other , a comparison between these three classes should reveal something about the impact of the pandemic on student performance.
This research design has its flaws because assignment to treatment is not random. For example, the senior year of the class of 2021 had the added stress of a hectic election campaign and its violent aftermath. These additional stressors are potential confounds in this research design. But because we cannot randomly assign the impact of the pandemic on students' lives, a research design that compares across graduating classes may be as good as it gets.
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Last updated 6 Sept 2022
Different types of methods are used in research, which loosely fall into 1 of 2 categories.
Experimental (Laboratory, Field & Natural) & N on experimental ( correlations, observations, interviews, questionnaires and case studies).
All the three types of experiments have characteristics in common. They all have:
Note – natural and quasi experiments are often used synonymously but are not strictly the same, as with quasi experiments participants cannot be randomly assigned, so rather than there being a condition there is a condition.
These are conducted under controlled conditions, in which the researcher deliberately changes something (I.V.) to see the effect of this on something else (D.V.).
Control – lab experiments have a high degree of control over the environment & other extraneous variables which means that the researcher can accurately assess the effects of the I.V, so it has higher internal validity.
Replicable – due to the researcher’s high levels of control, research procedures can be repeated so that the reliability of results can be checked.
Lacks ecological validity – due to the involvement of the researcher in manipulating and controlling variables, findings cannot be easily generalised to other (real life) settings, resulting in poor external validity.
These are carried out in a natural setting, in which the researcher manipulates something (I.V.) to see the effect of this on something else (D.V.).
Validity – field experiments have some degree of control but also are conducted in a natural environment, so can be seen to have reasonable internal and external validity.
Less control than lab experiments and therefore extraneous variables are more likely to distort findings and so internal validity is likely to be lower.
These are typically carried out in a natural setting, in which the researcher measures the effect of something which is to see the effect of this on something else (D.V.). Note that in this case there is no deliberate manipulation of a variable; this already naturally changing, which means the research is merely measuring the effect of something that is already happening.
High ecological validity – due to the lack of involvement of the researcher; variables are naturally occurring so findings can be easily generalised to other (real life) settings, resulting in high external validity.
Lack of control – natural experiments have no control over the environment & other extraneous variables which means that the researcher cannot always accurately assess the effects of the I.V, so it has low internal validity.
Not replicable – due to the researcher’s lack of control, research procedures cannot be repeated so that the reliability of results cannot be checked.
Field experiments, laboratory experiments, natural experiments, control of extraneous variables, similarities and differences between classical and operant conditioning, learning approaches - social learning theory, differences between behaviourism and social learning theory, research methods in the social learning theory, our subjects.
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Humanities and Social Sciences Communications volume 11 , Article number: 84 ( 2024 ) Cite this article
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Low-carbon transition stands as a vital strategy for the global community to address the challenge of climate change, inevitably affecting residents’ daily lives. However, there is a notable gap in the quantitative analysis of the low-carbon transition’s impact on energy poverty in developing countries, limiting policymakers’ understanding of the inherent mechanism and their ability to take informed actions. This study investigates the low-carbon city pilot (LCCP) policy, China’s key low-carbon initiative, as a quasi-natural experiment, using the difference-in-differences (DID) method to examine its impact on residents’ energy poverty conditions. Utilizing panel data from 4807 households in the CHARLS dataset, this study effectively integrated household-level and city-level data. Benchmark regression indicates that the LCCP policy exacerbates energy poverty among residents. Further analysis reveals the pivotal role of energy infrastructure and expenditure in bridging the nexus between the LCCP policy and energy poverty, providing crucial insights into the potential pathways through which this policy impacts energy poverty. Additionally, heterogeneity analysis indicates that the impacts of LCCP policy are more pronounced in eastern cities, non-resource cities, and high administrative-level cities, as well as in the communities suffering from subpar governance quality. By leveraging reliable survey data and robust quantitative methods, this study not only broadens the methodology of energy poverty studies but also offers valuable insights for developing countries to safeguard residents’ energy welfare amid low-carbon transitions.
Introduction.
Low-carbon transition has been widely endorsed by the international community as a crucial lever to mitigate global warming (He et al., 2022 ; Olabi and Abdelkareem, 2022 ). Currently, global efforts in the low-carbon transition have transformed energy structure and bolstered the use of clean and renewable energy, thus aiding in achieving carbon reduction goals (Yu et al., 2022 ; Zhang et al., 2022 ). However, in light of the classic “energy trilemma” predicament, efforts toward low-carbon transition, at times, have unintentionally impacted energy security and energy equity in certain regions (Mišík, 2022 ; Xie et al., 2022 ). As countries implement these low-carbon strategies, their energy systems and even whole socioeconomic systems have become increasingly unstable and vulnerable (Frilingou et al., 2023 ; Magacho et al., 2023 ; Semieniuk et al., 2021 ; Sovacool et al., 2019 ). During the COVID-19 pandemic and the exacerbation of geopolitical tensions, various countries have witnessed energy supply threats and energy market fluctuations, further intensifying the energy accessibility challenges for numerous populations (Belaïd, 2022b ; Carfora et al., 2022 ). Recent data reveals a startling 20% increase in the global population lacking sufficient energy service in daily life (Siksnelyte-Butkiene, 2022 ). Consequently, both scholars and policymakers must recognize the unforeseen repercussions of the low-carbon transition, particularly its implications for vulnerable groups in developing countries.
When residents grapple with challenges in getting enough energy services to sustain their daily lives, they are defined as trapped in an energy poverty condition (Liang and Asuka, 2022 ; Sy and Mokaddem, 2022 ). As the primary indicator assessing a resident’s energy welfare, energy poverty encompasses the difficulties residents face in accessing or affording fundamental modern energy services (González-Eguino, 2015 ; Nussbaumer et al., 2012 ). According to previous studies, energy poverty, underscored by indoor air pollution and diminished thermal comfort, disrupts residents’ daily activities, severely affecting their physical and psychological well-being (Xiao et al., 2021 ; Zhang et al., 2021 ). Furthermore, it also leads to a decline in productivity, thereby potentially exacerbating social inequities and hindering development in disadvantaged regions (Du et al., 2022 ; Liu et al., 2022 ; Shahzad et al., 2022 ). Recognizing the gravity of this issue, the United Nations ( 2012 ) considers universal access to modern energy services as a major goal by 2030.
Scholars have approached the tension between low-carbon transition and energy poverty from perspectives of equity and justice (Heffron, 2022 ). Since related policies were mainly formulated and executed by predominant governmental and corporate entities, the voice of the general populace is marginalized, further obstructing the realization of distributive, recognition, and procedural justice (Sovacool, 2021 ; Sovacool and Dworkin, 2015 ). During the low-carbon transition, on the one hand, the construction of wind/solar farms has encroached upon the arable lands that residents rely on for sustenance, exacerbating their impoverished conditions (Argenti and Knight, 2015 ; Gorayeb et al., 2018 ). On the other hand, such a transition has not only elevated the cost of energy production, transmission, and storage but also heightened the unpredictability of the energy system, inevitably increasing the risk of energy disruption and the economic burden of vulnerable groups (Geels et al., 2017 ; Mohseni et al., 2022 ; Tian et al., 2022 ). Recognizing the challenges the low-carbon transition posed, Belaïd ( 2022b ) has probed into the new forms of inequalities birthed by transition policies, offering an integrated framework for harmonizing the low-carbon transition and energy poverty governance in developing countries. Existing research advises policymakers to ensure residents’ welfare during the low-carbon transition, especially addressing the energy poverty issues confronted by vulnerable groups. Yet, current research still contains the following three gaps:
Firstly, previous studies on the impacts of the low-carbon transition on energy poverty often remain limited to qualitative discussions, lacking quantitative analysis. Secondly, academia primarily addresses the direct impact of the low-carbon transition, with a scant exploration into its underlying mechanisms or the heterogeneous effects under diverse governance scenarios. Thirdly, the focal point of most research predominantly rests on the developed countries, overlooking the specific challenges faced by vulnerable groups in developing countries. These research gaps hinder the governance implications of the pertinent conclusions, necessitating deeper exploration.
This study examines the relationship between low-carbon transition and energy poverty in developing countries, using China’s low-carbon city pilot (LCCP) policy as a quasi-natural experiment. Specifically, employing the difference-in-differences (DID) method, we assess the LCCP policy’s impact on residents’ energy poverty conditions. We use panel data from 4807 households containing middle-aged or senior members in the China Health and Retirement Longitudinal Study (CHARLS) and match the data with the LCCP policy implementation in China’s cities, shedding light on the macro-policy’s micro-impacts. Moreover, we explore the underlying mechanisms by which the LCCP policy exerts its impacts, emphasizing the two mediating variables, including energy expenditure and infrastructure. Lastly, we conduct a heterogeneity analysis to understand the policy’s impacts in cities and communities with different characteristics.
The study makes three significant contributions to existing literature. Firstly, this study offers a quantitative insight into the significant implications of low-carbon transitions on energy poverty in developing countries. With some cities in China adopting the LCCP policy and others yet to, China’s LCCP initiative emerges as an ideal quasi-natural experiment to probe the effects of such transitions (NDRC, 2014 ). While earlier scholars predominantly embraced qualitative analysis or case studies, this study conducts a deeper and more reliable analysis, providing quantitative evidence for the relationship between low-carbon transition and energy poverty (Ravigné et al., 2022 ; Upham et al., 2022 ). Secondly, this study innovatively combines city-level pilot policies with household-level data, examining the micro-impacts of macro-policy. In previous research, scholars either pursued macro analysis using regional data or probed individual factors impacting energy poverty using household data (Dong et al., 2021 ; Zhao et al., 2022 ). Anchored by reliable survey data and robust methods, this study broadens the methodology for energy poverty research. Finally, the quantitative analysis not only aids China’s policymakers in assessing the eventual impact of their LCCP policy on residents’ welfare but also provides valuable reference for developing countries charting their future low-carbon transition pathways.
The remainder of this paper is structured as follows. Section “Literature review, theoretical basis, and research framework” reviews existing literature and proposes the theoretical basis and research hypotheses. Section “Methodology and data” introduces the methodology, including the model construction, variable selection, and data source. Section “Results and discussion” presents the results, as well as a discussion of the main findings. Section “Robustness test” presents the robustness tests. Section “Conclusion and policy recommendations” summarizes the main conclusions and offers relevant policy implications.
Literature review, determinants of energy poverty.
Energy poverty, also called fuel poverty, is a central theme highlighting residents’ welfare, which has attracted increasing scholarly interest. Since Boardman pioneered the 10% indicator for the energy poverty condition in the United Kingdom, various standards like the 2M indicator (double the median share of household expenditure on energy), low-income high cost (LIHC) indicator, and minimum living costs (MIS) indicator have emerged to determine whether residents are living in energy poverty or not (Boardman, 1991a ; Castaño-Rosa et al., 2019 ; Hills, 2012 ; Moore, 2012 ). To fully cover residents’ daily energy needs, Nussbaumer et al. ( 2012 ), drawing inspiration from the Oxford Poverty and Human Development Initiative, introduced the multidimensional energy poverty index (MEPI), encapsulating a range of daily energy necessities, from cooking, heating, entertainment to communication. Furthermore, based on the LIHC indicator, Belaïd and Flambard ( 2023 ) integrated three aspects, including income, energy, and housing costs, presenting a more holistic conceptual framework. Scholarly refinements in energy poverty indicators lay a solid foundation for further analysis.
The determinants of energy poverty have been studied from macro or micro perspectives. At the macro level, factors like regional economic development, resource allocations, and technological development played pivotal roles in determining the energy poverty of certain regions (Liang and Asuka, 2022 ; Wang and Hao, 2018 ; Xiao et al., 2023 ). At the micro level, factors such as household income, age, educational level, as well as societal belief were found to be associated with residents’ energy poverty conditions (Awaworyi Churchill and Smyth, 2022 ; Belaïd, 2022a ; Belaïd and Flambard, 2023 ; Fry et al., 2022 ; Hasanujzaman and Omar, 2022 ). Yet, current studies focus predominantly on general factors, neglecting the impacts of government-led policies represented by the low-carbon transition. Such oversights limit the depth and clarity of insights into fluctuations in residents’ energy poverty conditions.
Although the low-carbon transition has engendered numerous positive effects for the societal ecosystem, researchers have begun casting light upon the trade-off between such a transition and residents’ welfare. As early as 1991, Boardman ( 1991b ) argued that the introduction of carbon tax policy in the United Kingdom could cast a shadow upon the welfare of impoverished households. In the process of implementing a low-carbon policy, if stakeholders fail to simultaneously enhance energy efficiency, some households may be triggered into the predicament of high energy expenditure (Ürge-Vorsatz and Tirado Herrero, 2012 ). Nguyen et al. ( 2019 ) revealed that as Vietnamese households progressed from traditional to modern energy systems, there was a marked escalation in expenditure-based energy poverty. In the solar energy industry, the fabrication of thin-film solar panels, while advantageous for certain regions’ low-carbon transition, also harbors potential health risks for manufacturing workers (Mulvaney, 2014 ). In fact, numerous endeavors aimed at energy transition, including architecture modifications, household solar panels, and electric vehicles, have precipitated varying degrees of discrimination and injustice among people, with a more conspicuous impact on vulnerable groups (Sovacool, 2021 ).
Diving deeper into the effects of the low-carbon transition on residents’ welfare, researchers have pursued comprehensive studies from the perspective of energy justice. Setyowati ( 2021 ) examined the Indonesian government’s efforts to achieve energy justice during the low-carbon transition and found that these endeavors inadvertently led to the further exclusion and disempowerment of energy-poor communities in energy-related decisions. In China’s context, Wang and Lo ( 2022 ) investigated the country’s journey toward justice during the energy transition, using the case of the environmental organization “Friends of Nature.” They suggested that China’s approach is distinctively different from the West, primarily based on Confucian self-cultivation. Sovacool et al. ( 2019 ) studied low-carbon initiatives in various countries, including France’s nuclear power, the UK’s smart meters, Norway’s electric vehicles, and Germany’s solar energy, and identified 120 energy injustices and introduced a strategic framework that includes distributive justice, procedural justice, cosmopolitan justice, and recognitional justice to ensure a fairer transition. While many scholars elucidate deprivation and inequity during the low-carbon transition by case studies, the lack of quantitative data makes it difficult to truly understand the degree to which certain low-carbon transition practices contribute to energy poverty.
As the world’s most populous developing country, China’s move toward a low-carbon transition might place a considerable burden on its residents (Bai et al., 2023 ). The “Coal-to-Gas” initiative launched in 2017 inadvertently resulted in a shortage of natural gas, leading to an inability for many households in northern China to heat their rooms (Luo et al., 2021 ; Wang and Ren, 2020 ). Furthermore, China’s environmental protection law (Ma et al., 2022 ), as well as local environmental regulations (Xiao et al., 2023 ), have intensified energy poverty issues, particularly for households dependent on non-clean energy. However, a comprehensive quantitative analysis of the impact of China’s low-carbon transition policy on residents’ energy poverty is still lacking.
China’s Low-Carbon City Pilot (LCCP) policy forms a critical part of the country’s broader low-carbon transition strategy (Yang et al., 2023b ). In pursuit of exploring efficient pathways towards carbon emission reduction, the National Development and Reform Commission selected cities to roll out the LCCP policy in 2011, 2013, and 2017. Directed by the central government, each pilot city, which reflected its own socio-economic characteristics, set individual carbon peaking objectives, established comprehensive greenhouse gas emission tracking systems, and employed both legal and economic mechanisms to encourage stakeholders to act accordingly (NDRC, 2014 ). The LCCP policy’s overarching ambition is to overhaul the energy framework, augment energy efficiency, and achieve tangible reductions in greenhouse gas emissions.
The LCCP policy demands more in-depth exploration regarding its implications for residents. However, academic investigations have predominantly focused on the policy’s broader outcomes, such as carbon emissions, ecological preservation, energy efficiency, innovation, and sustainable growth, highlighting its positive effects based on provincial or city-level data (Yang et al., 2023a ; Zhang, Feng, et al. 2022 ; Zhu and Lee, 2022 ). Previous studies risk overlooking the intricate impacts on residents’ energy welfare. Considering that residents utilize various forms of energy—like electricity, gasoline, and coal—accounting for around 20% of the overall societal energy usage (Shen and Shi, 2018 ), the implications of the LCCP policy on the energy system inevitably cascade down to residents, influencing their energy welfare.
Drawing upon existing research, this study centers on the theories of quasi-public goods and energy justice (Belaïd, 2022b ; Belaïd and Flambard, 2023 ; Xiao et al., 2023 ). Both theories, grounded in human rights perspectives, offer a qualitative explanation for the latent correlation between governmental actions toward low-carbon transition and the energy poverty conditions of residents.
The theory of quasi-public goods concerns those goods that lie between the private and public domains (Buchanan, 1965 ; Savas, 1999 ). Unlike clear-cut public or private goods, quasi-public goods are partly non-rivalrous and non-excludable. Currently, utilities such as energy, water, and communication exhibit characteristics of quasi-public goods, with energy being a prime example (Zhao et al., 2015 ). Energy is vital for residential life, requiring residents to bear associated costs for their daily consumption. However, the energy sector is largely dominated by suppliers who possess inherent monopolistic characteristics (Wang and Chen, 2012 ). Given that the infrastructures of electricity and natural gas in specific regions serve a multitude of users and are irreplaceable in function, residents face stark limitations in choosing suppliers and struggle to find better suppliers based on free-market principles. As governments advocate for low-carbon transitions, energy suppliers might face increased costs, raising terminal energy prices. Due to the monopolistic nature of the energy sector, residents cannot easily switch to cheaper alternatives, thus risking increased energy costs, supply interruptions, and subsequent energy poverty.
Energy justice, viewed as the “ethical turn” in current energy policies and related research, aims to address the marginalization of vulnerable populations in policy formulation and implementation (Hartwig et al., 2023 ). Instead of viewing energy policies solely as technical solutions to climate issues, energy justice sees energy systems as a socially embedded phenomenon calling for a politically and morally informed response (McHarg, 2020 ). This perspective underscores the importance of prioritizing vulnerable groups during the low-carbon transition and addressing the inherent injustices and inequalities (Bouzarovski and Simcock, 2017 ; Jenkins et al., 2021 ; Sovacool et al., 2023 ). McCauley et al. ( 2013 ) and Jenkins et al. ( 2016 ) initially framed energy justice in terms of distribution, recognition, and procedure. Later scholars have added restorative and cosmopolitan justice to this framework (Heffron, 2022 ). Given the quasi-public nature of energy, the impact of low-carbon transition on residents’ welfare is unavoidable. Energy justice enhances this argument, incorporating the justice dimension into the core values of governance, providing policymakers with a framework to identify and counter the ethical dilemma of low-carbon transition.
In summary, these theories provide an integrated consideration of climate, economy, and ethics for the formulation and implementation of energy policy. Quasi-public goods theory highlights the added burden residents face due to low-carbon transitions, while energy justice theory offers ethical benchmarks to address this issue. Using these theories as a foundation, this study investigates the nexus between low-carbon transitions and energy poverty in developing countries, utilizing quantitative analysis informed by China’s LCCP policy.
To fill the research gap, this study treats LCCP policy as a quasi-natural experiment and employs the DID approach to delve deeper into the impacts of LCCP policy on the residents’ energy poverty conditions, thereby advancing the understanding of the effects of low-carbon transition on energy poverty in developing countries.
Fundamentally, the LCCP policy is composed of a series of concrete emission reduction measures, forming a comprehensive policy system (Li et al., 2018 ; Wang et al., 2015 ). To meet stringent emission goals, local governments employ legal constraints and financial support to urge various stakeholders to reduce emissions, thereby driving the transformation of the societal energy structure (Feng and Chen, 2018 ; Khanna et al., 2014 ; Song et al., 2020 ). Although the main implementers of LCCP policy are the government and related enterprises, with few direct restrictions imposed on residents, residents will inevitably be affected by the aforementioned measures as the ultimate consumers of energy (Sovacool, 2021 ).
Primarily, the LCCP policy can exacerbate residents’ energy poverty conditions by increasing necessary living energy expenditure. On the one hand, in a bid to optimize industrial and energy structure, the government propels solar power, natural gas, electricity, and other advanced energy to supplant outdated energy sources such as coal (Li et al., 2018 ). Some archaic enterprises may even face constraints or closures, inevitably leading to an energy supply shortage. In fact, inherent governance defects have further intensified this shortage resulting from energy structure upgrading (Luo et al., 2021 ). In China, the domestic natural gas shortage and electricity shortage that occurred in 2017 and 2021, respectively, are concrete manifestations of this predicament. On the other hand, energy enterprises, in order to comply with government emission reduction requirements and ensure normal operation, may invest more funds into technology upgrades and facility renovations, thereby escalating energy production costs (Amores-Salvadó et al., 2014 ; Sarkis and Cordeiro, 2001 ). Consequently, these enterprises pass on these costs to consumers when providing energy services, causing residents to bear the economic cost of cities’ low-carbon transition (Zhang, 2018 ). In fact, energy prices have nearly doubled during some regions’ low-carbon transition, leaving residents facing severe energy poverty issues (Frondel et al., 2015 ).
However, it is necessary to note that modern energy infrastructures established by the LCCP policy could potentially alleviate residents’ energy poverty conditions. During policy implementation, governments encourage enterprises and other stakeholders to construct modern infrastructures for energy production, transmission, and distribution (Li et al., 2018 ). In China, as a result of the construction of large-scale power grids and natural gas networks, numerous residents have transitioned from using solid fuels such as coal or straw to modern energy (Yang et al., 2020 ). Previous research has demonstrated that well-developed energy infrastructures are crucial prerequisites for residents to get rid of energy poverty (Lippert and Sareen, 2023 ). Thus, energy infrastructure should also be taken into consideration when exploring the impact of LCCP policy on energy poverty.
Given the above analysis, the exact impacts of LCCP policy on energy poverty and the intermediary mechanisms still warrant further exploration. Therefore, we propose three hypotheses as follows, and the impact path is shown in Fig. 1 .
Impact path of the LCCP policy on energy poverty.
Hypothesis 1: The LCCP policy exacerbates residents’ energy poverty condition .
Hypothesis 2: The LCCP policy exacerbates residents’ energy poverty condition through increasing energy expenditure .
Hypothesis 3: The LCCP policy alleviates residents’ energy poverty conditions through energy infrastructure construction .
Model construction, general form of difference-in-differences model.
The implementation of specific public policies may impact certain groups while leaving other groups unaffected. Thus, it can be likened to a particular “treatment” administered to subjects in a medical experiment. Much like research in natural sciences, events in social science studies that alter the environment of individuals or cities in society are often referred to as quasi-natural experiments. If a specific public policy is seen as a quasi-natural experiment, then by comparing the individuals affected by the policy (treatment group) with the individuals unaffected (control group), one can discern the effects brought forth by the policy (Zhou and Chen, 2005 ).
The DID method is often employed to investigate the effects of public policy implementation from the perspective of quasi-natural experiments. Specifically, the DID method uses the dual differences in cross-sections and time series introduced by the public policy to identify the policy’s “treatment effect” (Zhou and Chen, 2005 ). Its merit lies in circumventing the endogeneity issues when using policy as an explanatory variable and effectively controlling the interaction between dependent and independent variables. The DID model with panel data can account for unobservable individual heterogeneity among samples and control for unobservable factors that change over time, thereby achieving an unbiased estimation of policy effects (Fan et al., 2017 ). The general form of the DID model is shown in Eq. ( 1 ). Herein, \(y_{it}\) represents the dependent variable. The interaction term \(\left( {G_i \times D_t} \right)\) indicates if the region of residence for individual i implemented a specific policy in year t . A value of 1 confirms this, while 0 negates it. \(X_{it}\) includes control variables that could impact the dependent variable. μ and ε , respectively, represent the fixed effect and the error term.
The objective of this study is to delve into the impact of LCCP policy on residents’ energy poverty conditions. Drawing from previous analysis, the effect of the LCCP policy can be perceived as a quasi-natural experiment. Given that selected pilot cities implemented the LCCP policy, their residents are inevitably under its sway. Conversely, residents of no-pilot cities remain unaffected. Thus, residents in pilot cities can be categorized as the treatment group, and those in non-pilot cities can be categorized as the control group. Utilizing the DID method, we can scrutinize the impact of LCCP policy by investigating differences before and after policy intervention, as well as differences between treatment and control groups at the same time point (Q. Shen et al., 2023). The benchmark DID model is shown in Eq. ( 2 ).
Herein, i and t denote specific residents and years, respectively. \({\rm {MEPI}}_{it}\) signifies the energy poverty condition experienced by resident i in the year t . \({\rm {LCCP}}_{it}\) denotes whether the city where resident i lives implemented the LCCP policy in the year t , and a value of 1 indicates affirmation, whereas 0 indicates negation. \(C_{it}\) embodies control variables that could impact the residents’ energy poverty. \(\mu _i\) and \(\sigma _t\) correspondingly represent the fixed effects of residents and years, while \(\varepsilon _{it}\) constitutes the error term. In this model, the coefficient \(\beta _1\) captures the shock of LCCP policy on energy poverty, with a positive value indicating an exacerbation effect, a negative value indicating an alleviation effect, and an insignificant value suggesting no substantial impact.
Regarding the intermediary effects of energy expenditure and energy infrastructure, we construct the following model, as depicted in Eqs. ( 3 ) and ( 4 ), to delve into the intermediary mechanisms.
In this model, \({\rm {Mediat}}_{it}\) represents the mediating variables. The coefficient \(\beta _1\) captures the impact of LCCP policy on mediating variables, while the coefficient \(\beta _4\) captures the impacts of mediating variables on residents’ energy poverty. A statistically significant value for both coefficients indicates the existence of intermediary effects, while an insignificant value suggests no such effect.
When examining the impact of the LCCP policy on the energy poverty of residents, it is imperative to meet the following two fundamental prerequisites: (1) Random City Selection for Pilots : The process of selecting low-carbon pilot cities should be random, free from biases that might affect the dependent variable. Current literature and official statements suggest that policymakers have not considered residents during pilot city selection (Deng and Zhan, 2017 ). Our analysis of energy poverty conditions across low-carbon pilot cities shows varied values, indicating that city selection is random to some extent. (2) Parallel trends : Prior to the implementation of the LCCP policy, residents’ energy poverty conditions in pilot cities should have a similar trend as those in no-pilot cities. This will be further elaborated upon in the section “Parallel trend test”.
Dependent variable.
Residents’ energy poverty condition serves as the dependent variable in this model, referring to the challenges residents confront in accessing or affording modern energy services. We adopt the multidimensional energy poverty index (MEPI) framework, the widely accepted measurement proposed by Nussbaumer et al. ( 2012 ), to measure residents’ energy poverty condition (Zhang, Appau et al., 2021 ). Specifically, we refine some indicators of MEPI to reflect China’s unique circumstances more precisely. Finally, we developed a modified MEPI indicator system, including five dimensions (cooking, room temperature, household appliances, education/entertainment, and communication) and 10 specific indicators. Considering each dimension holds significant importance in household living, we assign each dimension an equal weight of 0.2 (Zhang et al., 2019 ). However, for indicators within each dimension, we employ the entropy method to assign weights, thereby avoiding subjective biases within specific dimensions (Feng et al., 2022 ; Zhang, Shu et al., 2021 ). The MEPI indicator system and corresponding weights of indicators are shown in Table 1 .
According to the MEPI indicator system in this study, if a household’s condition meets the criterion for residents’ energy poverty, we will assign the indicator value to 1; otherwise, it will be assigned to 0. Specifically, if a household (1) uses non-modern energy sources (coal, straw, etc.) in cooking; (2) has no air conditioning; (3) has poor thermal comfort (too cold or hot); (4) has no refrigerator; (5) has no washing machine; (6) has no hot water supply; (7) has no television; (8) has no computer; (9) has no mobile phone; (10) has no internet, the corresponding indicator’s value is assigned to 1. Finally, these values are aggregated according to their respective weights to calculate the final MEPI, as shown in Eq. ( 5 ). The higher the MEPI of the residents’ households, the more severe their energy poverty condition.
The LCCP policy serves as the independent variable within this model. As previously mentioned, when a specific city was chosen as an LCCP pilot in a certain year, the variable LCCP for that year and all subsequent years will be assigned to 1; otherwise, it will be assigned to 0. China’s LCCP policy has undergone three batches: the first batch commencing in 2011, the second in 2013, and the final batch in 2017. The first batch was primarily aimed at provincial administrative regions, while the third batch had an excessively brief duration, both being unsuitable for this study (Zhao and Wang, 2021 ). Hence, this research selects the second batch of low-carbon pilot cities as a treatment group, while cities not identified as low-carbon pilot cities are utilized as a control group. In consideration of the availability of household-level data from the CHARLS database, 13 cities were finally chosen as the experimental group, and 85 cities as the control group.
Energy expenditure is a mediating variable. Within China’s economic situation, the price of transportation fuels, such as petrol, often fluctuates due to market dynamics (Ju et al., 2017 ). In contrast, residential electricity prices largely retain their stability, primarily due to governmental constraints (Li et al., 2023 ). Consequently, for a household, expenditures on domestic electricity can function as a reference benchmark, while expenditures on transportation might effectively serve as an indicator reflecting energy price fluctuations. Accordingly, we utilize the ratio between the transportation fee and the electricity fee of a household to measure energy expenditure.
Energy infrastructure is another mediating variable. Regarding infrastructural developments in China, natural gas, an innovative fuel advocated by governments in recent years, its pipeline construction can serve as a relatively precise barometer of the progress in energy infrastructure (Dong, Jiang et al., 2021 ; Dong et al., 2017 ). Thus, we utilize household natural gas supply as a measurement of energy infrastructure.
Eight control variables are incorporated at the city level and household level, thereby enhancing the accuracy of our parameter estimates and alleviating biases derived from omitted variables. In light of previous research, at the city level, we incorporate variables including economic development, population, industrial structure, and societal consumption (Dong et al., 2021 ; Ren et al., 2022 ; Zhao et al., 2022 ). Specifically, we (1) use per capita GDP to denote economic development, (2) use the year-end total population as a measure of population, (3) use the ratio of the secondary industry’s added value to GDP as a measure of industrial structure, and (4) use the total retail sales of consumer goods to represent societal consumption. At the household level, we include (5) household income, (6) household size, (7) marital status, and (8) the age of respondents (Abbas et al., 2020 ; Hong et al., 2022 ; Rahut et al., 2019 ).
This study utilizes household-level data from the China Health and Retirement Longitudinal Study (CHARLS) conducted by Peking University in collaboration with other institutions. This exhaustive survey employs a multistage stratified sampling methodology and rigorous survey process, guaranteeing regional representation and data quality (Peking University, 2023 ). CHARLS commenced its benchmark survey in 2011 and followed up in 2013, 2015, and 2018. The dataset encompasses households from 28 provinces, and more than 400 communities, offering rich information with a substantial sample size, fulfilling the requirements of this study.
CHARLS predominantly focuses on China’s households containing middle-aged or elderly members and collects household-level data, including income, consumption, and other routine activities. Considering the traditional Chinese family structure where middle-aged or elderly individuals often cohabitate with their offspring or kin, the CHARLS dataset aptly mirrors the typical Chinese household composition, portraying the evolving aging society in China (Wu, 2022 ; Yi and Wang, 2003 ). Therefore, if the energy poverty conditions of the households in CHARLS were confirmed to be impacted by LCCP policy, it would underscore the potential of low-carbon transition to alter energy poverty landscapes in developing countries. CHARLS publicly disclosed the cities where these households were located when starting the longitudinal survey. Leveraging this information, we can easily match these households with their respective cities, further establishing panel data to investigate the impact of the LCCP policy on residents’ energy poverty conditions (Li et al., 2022 ).
Our study incorporates household-level data from four waves of CHARLS surveys (conducted in 2011, 2013, 2015, and 2018) that maintained continuous tracking of these households. We utilize the primary characteristics and energy consumption data of these households for the dependent variable MEPI, mediating variables, and household-level control variables. Additionally, we gather city-level control variables—including per capita GDP, population, industrial structure, and societal consumption—from national and city statistical yearbooks.
Utilizing DID regression on household-level panel data, we surpass the scope of previous region-based studies, enabling us to capture dynamic processes at the micro level and thus facilitating a deeper analysis. Table 2 illustrates the variable measurements. Tables 3 and 4 provide the descriptive statistics and characteristics of key variables. To reduce heteroskedasticity, we apply logarithmic transformations (Numan et al., 2023 ) for variables including per capita GDP, population, societal consumption, and household income. Finally, we have collected panel data from 4807 households from the years 2011, 2013, 2015, and 2018, yielding a total of 19,228 observations. The MEPI for these households ranges between 0 and 1, with a mean value of 0.330, thereby delineating a representative snapshot of energy poverty among Chinese residents. These households are distributed across a range of city types, including 13 pilot cities and 85 non-pilot cities, thus offering a wide-ranging representation of the manifold city types within China.
The evolution of residents’ energy poverty condition.
Using the previously outlined MEPI indicator system, we are able to calculate the MEPI index for households and trace the energy poverty condition of 4807 households from 2011 to 2018. As depicted in Fig. 2 , the Sankey diagram illuminates the overall evolution of energy poverty within these sampled households, as well as the relative proportion of households experiencing varying degrees of poverty.
The evolution of residents’ energy poverty condition.
Upon a comprehensive overview in Fig. 2 , the period from 2011 to 2018 witnessed a gradual decline in severe-energy-poverty households with an MEPI over 0.75, paralleled by an increasing trend of no-energy-poverty households with an MEPI below 0.25. This implies a gradual alleviation of the overall energy poverty situation in China. However, throughout the 8-year interval from 2011 to 2018, despite the increasing number of no-energy-poverty households, there persistently existed a segment of originally no-energy-poverty households transitioning into light, moderate, or severe energy poverty during 2011–2013, 2013–2015, or 2015–2018. Particularly during 2013–2015, around 20% of originally no-energy-poverty households transitioned into light energy poverty, 7% into moderate, and 1% into severe energy poverty. The count of households transitioning into poverty during 2013–2015 exceeded that of any other interval before or after. This suggests a possible existence of an exogenous shock significantly impacting residents’ energy poverty conditions, which could likely result from several cities being designated as low-carbon pilots since 2013.
In the following section, we will employ the DID approach to explore whether the LCCP policy can lead to a change in residents’ energy poverty conditions.
Table 5 delineates the benchmark regression results of LCCP policy impact on energy poverty based on household-level panel data. Moving from column (1) to column (3), the coefficients of LCCP policy are significantly positive, irrespective of whether time-fixed or household-fixed effects are controlled. Furthermore, in column (4), when we simultaneously control both time-fixed and household-fixed effects, the coefficient of LCCP policy is 0.0218 at the 1% level. In other words, compared to the control group, the LCCP policy has exacerbated the energy poverty condition of residents in the pilot cities by 0.0218, thereby supporting Hypothesis 1. Sovacool et al. ( 2022 ) expound that the low-carbon transition is not a panacea devoid of detriments, and some actions towards low-carbon transition may indeed precipitate fresh inequities and risks. Our empirical analysis uncloaks the aggravating impact of the LCCP policy on residents’ energy poverty, viewed from the perspective of inhabitants’ welfare.
Control variables at both the city and household levels are incorporated into the DID model to mitigate omitted variable bias. The regression results in column (4) of Table 5 reveal that economic development (GDP), household income (INCOM), household size (HOUSIZE), and marital status (MARRIAG) exert significant influence on residents’ energy poverty conditions. Among these, higher economic development, higher household income, and larger household size serve to alleviate energy poverty, consistent with previous studies (Ren et al., 2022 ; Zou and Luo, 2019 ). Intriguingly, the absence of marital relationships appears to alleviate energy poverty, which could be explained from a feminist perspective: within married households, women are typically tasked with energy consumption-related domestic labor (Amigo-Jorquera et al., 2019 ; Robinson, 2019 ). However, women’s labor is often undervalued, leading to a lack of motivation within these households to upgrade their energy sources (Heltberg, 2005 ). In contrast, within unmarried or divorced households, women assume control of energy upgrades, thus effectively liberating themselves from energy poverty (Azhgaliyeva et al., 2021 ). In addition, the insignificance of other control variables might be attributed to complex nonlinear relationships (Yang et al., 2023a ).
The aforementioned regression confirms that the LCCP policy can exacerbate residents’ energy poverty conditions. Delving further, we elucidate the intermediary mechanism through the regression presented in Table 6 . Columns (1) and (2) scrutinize the mediating effect of energy expenditure, columns (3) and (4) scrutinize the mediating effect of energy infrastructure, whereas column (5) gauges the joint impact of both on energy poverty. Results indicate that both energy expenditure and infrastructure play significant intermediary roles, while their effects are diametrically opposed. On one hand, the LCCP policy significantly enhances energy expenditure, subsequently exacerbating energy poverty. Hypothesis 2 is thus confirmed. On the other hand, the policy bolsters the construction of energy infrastructure, thereby alleviating energy poverty, and Hypothesis 3 is verified. Taken together, LCCP policy could exacerbate energy poverty, which is consistent with the previous benchmark regression.
This study encompasses 98 cities in China. Cities located at different geographical positions exhibit substantial variations in their resource endowment, scales, and administrative levels. To delve deeper into whether the LCCP policy’s impacts differ across cities with distinct characteristics, we conduct a comprehensive heterogeneity analysis as follows.
Cities’ natural conditions, including geographical location and resource endowment, are taken into consideration. Cities are categorized into eastern, central, and western regions, referenced from previous studies (State Council, 2000 ; Zheng and Shi, 2017 ). Subsequently, cities are bifurcated based on their resource endowments into non-resource and resource-dependent cities, in alignment with the National Resource-based City Sustainable Development Plan issued by the State Council ( 2013 ). The regression results are represented in columns (1)–(5) of Table 7 .
The implementation of the LCCP policy in China’s eastern region could markedly intensify energy poverty, with a significant increase of approximately 0.0425 at a 1% level. Yet, this policy’s impacts on energy poverty in the central and western regions remain negligible. As the most economically vibrant region of China, the eastern region exhibits a keen response to supply-demand dynamics in energy pricing (Cai et al., 2023 ; He et al., 2016 ). Consequently, policy shifts have a swift and palpable impact on energy consumption at the household level. In contrast, the central and western regions with lower levels of economic development and marketization (Ren et al., 2018 ), exhibit a certain “inertia” in energy prices, and the energy poverty condition of residents in these regions also tends to remain unchanged during LCCP policy implementation.
In non-resource cities, the LCCP policy significantly exacerbates energy poverty, with a coefficient of 0.0345, whereas this impact is not significant in resource-dependent cities. Non-resource cities rely on imported energy from other cities or regions, which extends the energy supply chain and escalates acquisition costs (Qiu et al., 2021 ). Consequently, the disruption to their energy supply and household energy consumption by LCCP policy is more pronounced. On the other hand, resource-dependent cities usually satisfy their energy needs locally or nearby, ensuring shorter supply chains and swift demand response, further effectively mitigating the LCCP policy’s impact on the entire energy system and residents’ energy poverty. Interestingly, most resource-dependent cities are located in central and western China, while non-resource cities are chiefly located in the east, and the regression results for these two city types could offer mutual corroboration. Broadly speaking, non-resource cities, particularly those in the east, should be cautious when implementing the LCCP policy, paying keen attention to the energy welfare of their residents.
Heterogeneity analysis of cities’ social conditions, including administrative level and city scale, is also conducted. Cities are classified by administrative levels: high-level (sub-provincial city or municipality) and low-level (prefecture-level city). Furthermore, we partitioned cities into small (populations under 5 million), medium (populations between 5 and 10 million), and large (populations over 10 million), and the corresponding regression results are presented in columns (1)–(5) of Table 8 .
As shown in Table 8 , the impact of LCCP policy is significant in high-level or big cities, in contrast to low-level or small cities. The above two regressions can be explained together: high-level city or large city tends to be more developed, leading its residents to adopt large amounts of modern energy (Liu et al., 2012 ; Ouyang and Hokao, 2009 ). However, the energy composition of these cities is relatively monolithic, largely relying on single sources such as electricity or natural gas, with limited options for energy substitution. Overdependence on single sources risks plunging these cities’ residents into energy poverty during supply fluctuation caused by LCCP policy. Conversely, small cities with low administrative levels, despite some degree of energy poverty, exhibit a broader energy composition in residents’ daily lives, including electricity, natural gas, liquefied petroleum gas, biogas, etc. (Cui et al., 2019 ; Peidong et al., 2009 ), thus these residents’ energy poverty conditions are less sensitive to the LCCP policy targeted to the specific type of energy.
349 distinct communities are included in this study. As the fundamental administrative unit in China’s society, the community is linked to every resident’s daily life. The LCCP policy’s impact could vary significantly across communities with diverse characteristics. Initial surveys by CHARLS exhaustively charted the inherent features of communities, providing a complete dataset for community heterogeneity analysis.
From the perspective of community governance, communities are stratified based on public service quality (high or low, dependent on whether officials can speak Mandarin or not), and public expenditure (high or low, dependent on whether it exceeds the 20,000 Yuan threshold). The regression results are outlined in columns (1)–(4) of Table 9 . The regression results show a significant impact of the LCCP policy, which amplifies residents’ energy poverty in communities with low public service quality and low public expenditure. This suggests that the impacts of the LCCP policy vary with changes in community governance. In simpler terms, when grassroots governance is inadequate, the negative impacts of the LCCP policy become significantly more prominent. Grassroots governments, such as community administrators, serve as a ‘shield’ in mitigating potential energy poverty risks among residents during the low-carbon transition (Martiskainen et al., 2018 ).
In addition, the regression analysis presented in columns (5) and (6) of Table 9 reveals contrasting impacts of the LCCP policy on residents of urban and rural communities. Specifically, while the impact on urban residents’ energy poverty proves insignificant, it is significant in rural communities. These findings align with previous heterogeneity analyses of public service quality and public expenditure. The significant urban-rural gap and governance practice in China give urban residents an advantage in accessing abundant resources and favorable energy policies, thereby enabling them to mitigate the potential deleterious effects of the LCCP policy (Lu et al., 2022 ; Yao and Jiang, 2021 ). Conversely, residents in rural areas, especially those in remote and sparsely populated regions, are often overlooked by energy policymakers, leaving them at the lower end of the energy ladder (Li and Ma, 2023 ; Tang and Liao, 2014 ). Despite China’s recent progress made through “Targeted poverty alleviation” policy, which has lifted many rural residents out of absolute poverty, the existing rural energy infrastructure, including natural gas networks and power grids, is still inadequate for meeting residents’ daily energy needs (Li et al., 2019 ; Liu and Mauzerall, 2020 ). Consequently, during the supply shortfalls caused by LCCP policy, rural residents are often forced to resort to outdated energy sources like coal, exacerbating their plunge into energy poverty.
This research employs the DID method to delve into the impact of the LCCP policy on residents’ energy poverty conditions and its underlying mechanisms. Our findings offer valuable insights into the delicate tension between low-carbon transitions and energy poverty in developing countries, enriching the understanding of both scholars and policymakers.
This study analyzes 4807 continuously tracked household samples from the CHARLS dataset, offering a snapshot of China’s diverse households. Specifically, 79.08% of these households are married, and 78.75% have up to four members—a reflection of the smaller family units after China’s one-child policy in the 1980s. Approximately 50% of households reported a per capita income above 4000 Yuan, a figure that rose between 2011 and 2018, echoing China’s economic growth. However, the 8-year CHARLS survey reveals that, although there was an overall decrease in energy-poverty households from 2011 to 2018, some households transitioned into energy poverty. While broader studies suggest that China’s recent socio-economic growth has lessened its energy poverty issues (Liang and Asuka, 2022 ; Zhao et al., 2021 ), our analysis uncovers subtle ‘shadows’—households at risk of returning to energy poverty—overlooked in regional data.
This study found that the LCCP policy significantly exacerbated residents’ energy poverty condition, providing the first quantitative demonstration of the LCCP’s negative impacts at the household level. Our findings contrast with previous studies (Dong et al., 2021 ; Dong, Ren et al., 2021 ). Employing province-level data and general regression methods, they deduced that low-carbon transition mitigated energy poverty (Dong, Jiang et al., 2021 ). However, such regional data inadequately captures the intricacies of residents’ energy poverty. Additionally, gauging low-carbon transition via natural gas consumption fails to directly represent the overall implementation of the low-carbon transition policies, thus affecting the reliability of associated conclusions. Complementing earlier research, our study harnesses the LCCP—most representative low-carbon policy in China—to directly probe its consequences on residents’ energy poverty, yielding more precise conclusions. This beckons policymakers to weigh the possible ramifications on residents’ energy welfare in upcoming low-carbon endeavors and advises circumspection before embracing unreviewed low-carbon strategies.
This study experimentally identifies two potential mediating pathways in the relationship between LCCP policy and energy poverty: energy infrastructure and energy expenditure. Regression results reveal that LCCP policy can alleviate energy poverty through the enhancement of energy infrastructure, but exacerbate it by escalating energy expenditure. This can be explained as follows: To comply with government mandates regarding the LCCP policy, energy enterprises must augment their investments in infrastructure, refining energy production, and transportation, which subsequently elevates the cost of energy supply. These surging costs are then passed on to residents, subjecting households sensitive to energy price fluctuations to the energy poverty trap. Compared with previous research, this study delves into the relationship between variables utilizing household-level data, significantly augmenting scholars’ preliminary qualitative analysis on the ramifications of low-carbon transition for resident welfare. Earlier investigations indicated that, with the rise in natural gas and oil prices, households previously affording these energy forms have resorted to coal as an alternative (Kapsalyamova et al., 2021 ; Turdaliev and Janda, 2023 ). This research further elucidates the trend of residents downgrading their daily energy source due to escalating prices, linking this argument to the broader issue of energy poverty.
However, some scholars, adopting a system dynamics perspective, underscore the dynamic feedback interplay between the aforementioned variables, including low-carbon transition, energy expenditure, and energy poverty (Che et al., 2023 ; Venkateswaran et al., 2018 ). Che et al. ( 2023 ) created causal loop diagrams to capture the interplay between energy poverty and various socio-economic factors, accentuating that energy poverty is influenced not merely by an array of factors and multifarious pathways but also exerts its own influence on the broader system. These perspectives highlight a limitation of this study: the path we identified from the LCCP policy through energy expenditure to energy poverty, perhaps reflects the associations among variables rather than the direct causality. Nonetheless, our study offers valuable insights for policymakers seeking to intervene in the adverse impacts of low-carbon transitions.
Heterogeneity analyses reveal that eastern cities, non-resource cities, high-level cities, and larger cities manifest a pronounced risk of residents descending into energy poverty after LCCP policy enforcement. These cities typically have a vibrant energy market where energy supply is predominantly market-driven. Consequently, this study supports the notion that an active energy market can enhance energy poverty risks since energy service for residents is considered a quasi-public good (Xiao et al., 2023 ). This finding aligns with scholars who warn against unchecked marketization of quasi-public goods like energy and highlight the importance of sustained government oversight to ensure residents’ energy welfare (Luo, 2008 ; Zhao et al., 2015 ).
To ensure the reliability of DID regression, we conduct robustness tests, including parallel trends test, anticipation effects, placebo test, PSM-DID approach, outliers excluding, and variable substitution as follows.
The prerequisite for DID regression is the satisfaction of the parallel trend assumption (Liu et al., 2022 ; Zhao and Wang, 2021 ). In the context of our study, in the absence of the LCCP policy, the trend of energy poverty among residents in the pilot city should be similar to that of the non-pilot city. We employ Jacobson et al. ( 1993 ) method to perform the parallel trends test, as illustrated in Fig. 3 . The results reveal that the coefficient prior to the policy shock is close to zero and statistically insignificant, indicating no divergence between the pilot and non-pilot cities before policy implementation. The coefficients significantly rise to positive values when the policy is implemented, suggesting that the LCCP policy initially exacerbates energy poverty. However, the coefficients gradually decrease in the second and fifth post-implementation years, signaling a diminishing impact of policy. Overall, this method validates the parallel trends assumption.
Parallel trend test.
The absence of anticipation effects is another pivotal prerequisite for the DID method. If anticipation effects exist, they could cause estimation bias, making it difficult to determine whether the effects we observed in the treatment group are due to anticipation actions or actual policy implementation. Therefore, excluding anticipation effects is of utmost importance for our study. We will discuss the anticipation effects through two aspects: policy practice and data analysis.
Firstly, China’s pilot city policy is a conventional approach to policy exploration and policy learning (Wang and Yang, 2021 ). In China’s actual governance context, when selecting low-carbon pilot cities, the central government primarily considers regional representativeness (Fang, 2015 ), and the energy poverty condition does not fall into policymakers’ consideration. In previous quantitative studies, scholars have confirmed that the selection of low-carbon city pilots is not related to the cities’ own low-carbon development status before being selected (Deng and Zhan, 2017 ), indicating that the governments of pilot cities did not take relevant actions that may influence their conditions before LCCP policy implementation. Consequently, residents, at the furthest end of the policy impact scope, are even less likely to be prematurely affected. Therefore, based on the pilot-selection logic of the central government and previous studies, we have substantial grounds to confirm the absence of anticipation effects.
Secondly, we conduct a quantitative comparison, analyzing the average energy poverty condition in pilot cities and non-pilot cities before LCCP policy implementation. As shown in Fig. 4 , there are no significant differences between pilot cities and no-pilot cities when the LCCP policy has not been implemented. Specifically, the average energy poverty condition of all cities included in the study was 0.3494 in 2011. In pilot cities like Guilin and Suzhou, levels were lower than 0.3494, while in Hulunbuir and Ganzhou, levels were higher, presenting a relatively uniform distribution, similar to that in non-pilot cities, indicating no anticipation effects before policy implementation. Therefore, we can confirm the absence of anticipation effects.
Average energy poverty conditions of cities before policy implementation.
To mitigate the effects of random factors on energy poverty and substantiate the policy-driven impact, we conduct a placebo test through random sampling (Wang et al., 2023 ). We randomly select artificial pilot cities and policy implementation times from the samples, thereby randomizing the impact of the LCCP policy. We perform the corresponding DID regression and repeat the random process 500 and 1000 times, with the distribution of coefficients shown in Fig. 5 . The coefficients cluster around zero, markedly less than the previously estimated value of 0.0218. Most regression coefficients have p -values exceeding 0.1, indicating insignificance at the 10% level. Therefore, the LCCP policy’s impact on residents’ energy poverty is not accidental and is not influenced by other random factors.
Placebo test.
PSM-DID approach is used to counter the selection bias of the treatment group and reduce endogeneity issues (Dong et al., 2022 ). Initially, we conduct logit regression using control variables as covariates to calculate propensity matching scores. We then use the scores to match the treatment group and control group via nearest neighbor, radius, and kernel method, respectively. Lastly, we execute three DID regressions, as shown in Table 10 . The estimated values from all matching methods are similar to benchmark regression, confirming that the LCCP policy significantly exacerbates energy poverty, further reinforcing the robustness of our findings.
To mitigate the impact of outliers on the regression results, we apply a 1%, 5%, and 10% bilateral tail shrinkage treatment to the dependent variable. As shown in columns (1)–(3) of Table 11 , the coefficients of the LCCP policy are significant at the 1% level after this treatment. Simultaneously, we replace the dependent variable MEPI with cooking fuel type, another indicator of household energy poverty. The coefficient of the LCCP policy, as shown in column (4), remains significant. These findings thus substantiate the robustness of our conclusions.
To examine the relationship between low-carbon transition and energy poverty in developing countries, this study employs China’s LCCP policy as a quasi-natural experiment. Drawing from 4-year household survey data from CHARLS, we leveraged DID models to examine the impact of the LCCP policy on residents’ energy poverty conditions from a micro perspective.
The main conclusions are as follows: (1) The energy poverty conditions of the 4807 households involved in our study experienced notable shifts from 2011 to 2018, and a significant number of residents saw their energy poverty conditions worsen. (2) The DID regression underscores that the LCCP policy notably exacerbates residents’ energy poverty. This conclusion holds true even after various robustness tests, including parallel trend test, placebo test, PSM-DID, and other methods. (3) According to intermediary mechanism analysis, energy infrastructure and energy expenditure play critical roles in the relationship between LCCP policy and energy poverty, offering valuable insight into the potential pathways of LCCP policy’s impact. (4) City heterogeneity analysis shows that LCCP policy has stronger impacts in eastern, non-resource, larger, and high-level cities. In addition, community heterogeneity analysis underscores a more severe impact of the LCCP policy in communities with inadequate grassroots governance.
Considering the energy poverty issue brought about by the low-carbon transition in developing countries, this study illuminates the following policy implications for future low-carbon practices and energy poverty governance.
According to this study, there exists a delicate balance between advancing low-carbon transitions and ensuring residents’ energy welfare. Developing countries’ governments should adopt measured practices toward low-carbon transition, as well as assess the energy poverty risk of their residents. The empirical data presented in this study calls for a rethinking of current low-carbon strategies, represented by LCCP policy, and setting appropriate targets in light of local conditions. In practice, low-carbon policies that neglect residents’ welfare might not only lead to resource misallocation but also incite public opposition. For instance, when China’s “coal-to-gas” policy resulted in daily heating issues, the government was compelled to suggest a more flexible approach, prioritizing coal, electricity, or gas based on regional suitability. Such frequent changes in policy resulted in substantial wastage of both administrative and financial resources. Therefore, before embarking on future low-carbon-related policies, it is imperative for governments to meticulously evaluate the potential impact on residents’ energy welfare.
This study reveals the potential path of low-carbon transition impacting energy poverty: Regulations related to such transition invariably increase energy sector supply costs. These additional costs are transferred to final consumers, thereby increasing residents’ economic burden, and even worsening their energy poverty conditions. Thus, governments should pay close attention to energy price fluctuations during policy implementation, set up early warning mechanisms for energy price increasing and supply disruption, and take effective actions to protect households from these situations. Additionally, it is imperative for the government to provide financial support to households, lessening the economic pressure associated with the low-carbon transition. Given the unique nature of energy as a quasi-public good, the government should maintain its role as a “gatekeeper” of residents’ welfare, institutionalizing protections for the daily energy needs of residents, leveraging adaptive measures like universal service funds and housing renovation grants, thereby ensuring residents’ energy welfare during the low-carbon transition.
Beyond direct financial support, information support can also safeguard against the risks of energy poverty during the low-carbon transition. According to Kyprianou et al. ( 2019 ), Spain has begun to offer residents advice about energy services, including whether their energy contracts are suitable for their own needs, and how to improve household energy efficiency. Compared to the financial measures, information support measures, aimed at enhancing public awareness and enriching energy-service knowledge, provide a more economical way to alleviate energy poverty. Drawing from Spain’s policy, developing countries like China should also integrate such measures, which may yield long-term policy effects, into their policy frameworks. Additionally, our study reveals that well-governed communities can mitigate the potential impacts of low-carbon transition on residents’ energy poverty, highlighting the importance of community support. Therefore, governments should recognize community officials as key participants in energy poverty governance, acting as a bridge for the government to provide information support to the residents. Moreover, community officials can also collect residents’ feedback about their living conditions, and provide invaluable first-hand data for optimizing existing strategies.
Finally, this study also highlights the heterogeneous impacts of low-carbon transition across varied city characteristics, suggesting that governments should consider the specific socio-economic condition disparities of regions. Previous studies have shown that, compared with state-led governance for energy poverty, regional autonomy governance contained more measures directed at vulnerable consumer groups (Kyprianou et al., 2019 ). In other words, when regions have more administrative power to design their policies, they are more likely to implement diverse strategies that are better suited to local conditions. Therefore, considering the regional heterogeneity in China, it is necessary for the central governments to delegate the formulation of action plans to local governments. For instance, in bustling metropolises reliant on energy imports, local governments should establish mechanisms to monitor and regulate energy supply, ensuring its continuity and stabilizing energy prices for residents during market fluctuations. In less-developed yet resource-rich cities, local governments should focus on developing modern energy infrastructure accessible to vulnerable groups, ensuring they have access to efficient energy sources.
Original data for this study are available in the China Health and Retirement Longitudinal Study: http://charls.pku.edu.cn/ .
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This work was supported by the Ministry of Education of Humanities and Social Science project (No. 21YJC630022), and the China Postdoctoral Science Foundation funded project (No. 2023M743362).
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Xiao, Y., Feng, Z., Li, X. et al. Low-carbon transition and energy poverty: quasi-natural experiment evidence from China’s low-carbon city pilot policy. Humanit Soc Sci Commun 11 , 84 (2024). https://doi.org/10.1057/s41599-023-02573-2
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This study examines the effectiveness of price limits using a quasi-natural experiment in China, where ChiNext stocks’ daily price limits changed from 10 to 20%. The empirical results show asymmetric performance of the upper and lower limits. Widening the upper limit range can alleviate delayed price discovery and trading interference, whereas an equivalent lower limit can exacerbate these adverse effects. A wider upper limit range increases volatility spillovers but a wider lower-limit range does not. Such asymmetry is more pronounced when there is higher investor sentiment, a greater possibility of manipulation, and eligibility for short selling. Additional analyses suggest that widening the limit range provides investors with a greater opportunity to buy (sell) more on the upper (lower) limit hitting day and sell (buy) more on the following day, resulting in a greater order imbalance primarily caused by institutional investors. The results indicate that the daily price limit leads to market inefficiencies when the price rises but reduces stock price crashes and acts as a price stabilizer.
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Do price limits help control stock price volatility.
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Deb et al. ( 2010 ) and Kim and Park ( 2010 ) analyze major global markets and provide a rationale for implementing price limit systems in high regulatory risk markets with more irrational investors. Chen et al. ( 2005 ) document the asymmetric effectiveness of price limits in bullish and bearish periods. Chen et al. ( 2024 ) show that the effect of circuit breakers on overall welfare varies with investor motives.
Many capital markets worldwide have encountered the costs associated with price limits. Studies have identified these costs in various stock exchanges. In Europe, examples include the Spanish (Kim et al. 2008 ) and Athens (Phylaktis et al. 1999 ) stock exchanges. In Asia, significant effects have been observed in exchanges like Tokyo (Kim and Rhee 1997 ), Taiwan (Huang et al. 2001 ; Kim and Limpaphayom 2000 ), South Korea (Berkman and Lee 2002 ), and Shenzhen and Shanghai in China (Chen et al. 2019 ; Hou et al. 2020 ), among others.
Amidst a market crash, the selling pressure predominantly targets stocks with higher market capitalization, as highlighted by Lauterbach and Ben‐Zion ( 1993 ). Stocks that are easily manipulated are more inclined to be sold on the day when the lower limit is hit, aiming to mitigate further losses.
There is less discussion about the effectiveness of lower limit hits than that on upper limit hits generally. This is partly because lower limit hits exhibit similar characteristics to upper limit hits (Kim and Rhee 1997 ) or due to relatively insufficient sample data for lower limit hits (Kim et al. 2013 ).
Mostly, no price limit is imposed on new shares on their first listing day. Since December 13, 2013, a 44% price limit has been implemented for new shares on the first trading day, which is not applicable to new shares on the ChiNext market after August 24, 2020, or stocks on STAR. For more discussion on IPO pricing, see Qian et al. ( 2022 ).
“ST” stands for special treatment in the context of the Shanghai and Shenzhen Stock Exchanges’ Listing Rules. This status is applied to companies facing unusual financial situations or other exceptional circumstances that might lead to delisting, or when the company’s future becomes uncertain, posing a risk to investor rights. Typically, a company receives the ST designation if it reports negative net income for two consecutive years, signaling heightened risk to investors.
In the initial five trading days following their listing, newly listed shares on the ChiNext market are not subject to any price limits.
The empirical results using the full sample are represented in Panel A in Internet Appendix B . The results using the full sample have higher significance than those using the PSM sample. The results using the matching sample with more covariates are represented in Panel B in Internet Appendix B .
For stock price experiencing “no change” by definition, I define Continuation i,t as zero. Since the occurrence of no-change price behavior is infrequent, the results remain unaffected regardless of whether “no change” is categorized as “continuation” or “reversal.”.
Since the regression sample is not a panel dataset, firm fixed effects are not controlled in the main regression. See Panel C in Internet Appendix B for the results of controlling firm fixed effects.
Because the primary tests for the three hypotheses contain different sample observations, the number of observations reported in Panel B represents the total number of all observations for control variables during the sample period. 12,545 is the number of quarterly observations, and 712,710 is the number of daily observations.
The number of observations for each subgroup is inadequate when the price movement margin of 1% is used, especially for the ChiNext market after the event date. Internet Appendix C reports the results using a 1% price movement margin to classify stocks. The significance of the regressions weakens to some extent, which may be because of the scarcity of the observations.
The results of the univariate tests conducted over a 21-day event window, spanning from Day -10 to Day + 10, are detailed in the Online Appendix. Specifically, Internet Table D1 presents these results with TradeInterfer as the dependent variable, whereas Internet Table D2 focuses on Volatility as the dependent variable.
The results of Eq. ( 2 ) over the 21-day period are presented in Appendix 2. For the upward price movement, Columns (1) and (3) present the coefficients of Post × GEM × Dum20 ( β 11 ) and Post × GEM × Dum16 ( β 7 ), and Columns (2) and (4) present their t-values. From Day 1 to Day 4, β 11 in Column (1) is significantly positive on Day 1 and Day 2, close to the significance levels on Days 3 and 4, whereas β 7 in Column (3) is insignificant during the post-limit period, indicating a wider upper price limit increases the spillover of stock volatility up to four days after the price limit hit. However, for the lower price limit, β 11 in Column (5) is not significant during the post-limit period, indicating that a wider lower price limit does not affect stock spillovers. On Day 1, β 11 in Column (5) exhibits a negative value, with a t-value of -1.62. This indicates even a decrease in volatility spillover after widening the lower price limit range.
Through an analysis of the market index and investor sentiment, I distinguish between bullish and bearish market periods. The patterns depicted in Fig. 3 in Appendix 3 indicate that both the market index and investor sentiment experience higher (lower) values after (before) the event date, suggesting a bullish (bearish) market period following (preceding) the event date.
Naturally, this effect exists on the ChiNext board like other confounding events as well. However, applying a difference-in-differences approach guarantees the results are not affected.
The findings of delayed price discovery for the other two subgroups ( S 0.08 /S 0.18 and S 0.06 /S 0.16 ) are presented in Internet Appendix A . There is no price delay observed for stocks in the two subgroups during upward price movements, as shown in Internet Table A1 . However, the ChiNext and non-ChiNext stocks both exhibit price delays during downward price movements after the event date, as presented in Internet Table A2 . Moreover, stocks with wider price movement range show a significant price delay, which is consistent with the results of lower limit hits, indicating that a wider downward limit range exacerbates the price delay.
Post + 0 ( Post + 1 ) equals one when a stock-day observation falls in the time range from August 24, 2020 to August 23, 2021 (August 24, 2021–August 23, 2022) and zero otherwise.
The samples here are segmented into four-year intervals, with each interval demarcated by August 24 as the annual dividing line.
Amihud is not incorporated as a control variable in this regression.
I replaced the dummy variables Dum20 and Dum16 in Eq. ( 2 ) with the continuous variables Return20 and Return16 . When Dum20 and Dum16 are set to one, Return20 and Return16 take the corresponding stock returns; when Dum20 and Dum16 are set to zero, Return20 and Return16 also take the value of zero. This approach helps in analyzing the non-parametric possibilities of return changes. As only Eq. ( 2 ) allows for this kind of research design, I only examine the dependent variables TradeInterfer or Volatility when applying GAMs. The regression results are presented in Internet Appendix E . The empirical findings demonstrate that considering non-parametric possibilities does not alter the previously drawn conclusions.
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Siyuan Tang thanks for support from National Natural Science Foundation of China (Grant numbers [72102197]).
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See Fig. 3 .
Time-varying trends of market condition. This figure plots the time-varying trends in the SCI 300 index (black line) and investor sentiment (gray line) before and after widening the price limit range. The left-hand y-axis plots the SCI 300 index values for each trading month and the right-hand y-axis plots the investor sentiment values for each trading month. The x-axis plots the month relative to the event (August 2020)
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