metadata: authors: 0: author: Ravallion,Martin
count: World
docna: 0: docna: Can we trust shoestring evaluations ?
docty: Policy Research Working Paper
subtopic: Health Care Services Industry,Disease Control & Prevention,Poverty Impact Evaluation,Poverty Monitoring & Analysis,Gender and Development,Inequality,Poverty Assessment,Poverty Diagnostics,Poverty Lines,Small Area Estimation Poverty Mapping
teratopic: Macroeconomics and Economic Growth,Poverty Reduction,Science and Technology Development,Education,Communities and Human Settlements
abstracts: cdata!: Many more impact evaluations could be
            done, and at lower unit cost, if evaluators could avoid the
            need for baseline data using objective socio-economic
            surveys and rely instead on retrospective subjective
            questions on how outcomes have changed, asked
            post-intervention. But would the results be reliable? This
            paper tests a rapid-appraisal, "shoestring,"
            method using subjective recall for welfare changes. The
            recall data were collected at the end of a full-scale
            evaluation of a large poor-area development program in
            China. Qualitative recalls of how living standards have
            changed are found to provide only weak and biased signals of
            the changes in consumption as measured from contemporaneous
            surveys. Importantly, the shoestring method was unable to
            correct for the selective placement of the program favoring
            poor villages. The results of this case study are not
            encouraging for future applications of the shoestring
            method, although similar tests are needed in other settings.
repnme: repnme: Can we trust shoestring evaluations ?
display_title: Can we trust shoestring evaluations
listing_relative_url: /research/2012/03/15891196/can-trust-shoestring-evaluations
topicv3: Economic and Social Mobility m1326259 1152,Poverty m1326687 695,Injury m1327524 1428,Gender m1327621 615,Health m1504661 3480
publishtoextweb_dt: 2012-03-01T00:00:00Z
historic_topic: Macroeconomics and Economic Growth,Poverty Reduction,Science and Technology Development,Education,Communities and Human Settlements
no_of_pages: 24
author_keys: 0: author_key: 99002
model_extractions: WPS5983 Policy Research Working Paper 5983 Can We Trust Shoestring Evaluations? _Martin Ravallion_ The World Bank Development Research Group Director’s office March 2012
Policy Research Working Paper 5983

# **Abstract**

Many more impact evaluations could be done, and at lower unit cost, if evaluators could avoid the need for baseline data using objective socio-economic surveys and rely instead on retrospective subjective questions on how outcomes have changed, asked post-intervention. But would the results be reliable? This paper tests a rapidappraisal, “shoestring,” method using subjective recall for welfare changes. The recall data were collected at the end of a full-scale evaluation of a large poor-area development program in China. Qualitative recalls of how living standards have changed are found to provide only weak and biased signals of the changes in consumption as measured from contemporaneous surveys. Importantly, the shoestring method was unable to correct for the selective placement of the program favoring poor villages. The results of this case study are not encouraging for future applications of the shoestring method, although similar tests are needed in other settings.

This paper is a product of the Director’s office, Development Research Group. It is part of a larger effort by the World Bank to provide open access to its research and make a contribution to development policy discussions around the world. Policy Research Working Papers are also posted on the Web at http://econ.worldbank.org. The author may be contacted at mravallion@worldbank.org.

_The Policy Research Working Paper Series disseminates the findings of work in progress to encourage the exchange of ideas about development issues. An objective of the series is to get the findings out quickly, even if the presentations are less than fully polished. The papers carry the names of the authors and should be cited accordingly. The findings, interpretations, and conclusions expressed in this paper are entirely those of the authors. They do not necessarily represent the views of the International Bank for Reconstruction and Development/World Bank and its affiliated organizations, or those of the Executive Directors of the World Bank or the governments they represent._ Produced by the Research Support Team
# Can we trust shoestring evaluations?

## Martin Ravallion<sup>1</sup>

_Development Research Group, World Bank 1818 H Street NW, Washington DC, 20433, USA_

**JEL:** C81, H43

**Keywords:** Baseline survey, retrospective data, recall error, poor areas, China **Sector:** POV

> 1 These are the views of the author alone and should not be attributed to the World Bank or any affiliated organization. This paper builds on a long-term evaluation developed by the author and Shoahua Chen at the World Bank, in collaboration with staff of the Rural Survey Organization of China’s National Bureau of Statistics, which implemented the survey data collection. The author is also grateful to Solveig Buhl, then of Deutsche Gesellschaft für Technische Zusammenarbeit (GTZ), for comments on the recall module developed for this paper, and help in field testing and refining the module. Funding for the study was provided by the World Bank’s Knowledge for Change Trust Fund. For their comments, the author is grateful to Kathleen Beegle, Gero Carletto, David McKenzie and Dominique van de Walle.
# **1. Introduction**

There are a great many interventions that we would like to evaluate for which no baseline (pre-intervention) data are available. Think of all the development projects for which no impact evaluation was ever planned.<sup>2</sup> In the absence of baseline data we cannot do the standard ―doubledifference‖ estimator—comparing outcome changes since the baseline between treated and untreated units.

But there is a potential way out: We can ask post-intervention questions of both the treatment and comparison groups on how much their welfare has improved since the intervention began. This would dramatically lower the costs of impact evaluations—an example of what Bamberger et al. (2004) call ―shoestring evaluations.‖ And it would open up many new opportunities for learning about policy effectiveness. It could be especially helpful in addressing a common problem in impact evaluations of development projects, namely that the time period is often constrained to fall short of the period in which the full impact is to be expected (King and Behrman, 2009; Ravallion, 2009). For example, in evaluating donor-financed operations it can be hard to ensure that the impact evaluation extends far enough beyond the disbursement period to credibly capture the impacts.<sup>3</sup> Yet for certain types of development projects—including infrastructure—longer-term impacts are expected.

There have been examples of the use of retrospective questions to create ―instant longitudinal data‖ (Janson, 1990).<sup>4</sup> However, we know very little about the method’s performance in impact evaluations, where the interest is in comparing results from two samples, one treated and one not. The limited references one finds to the idea in the literature on evaluation appear to be encouraging. In their book, _Real World Evaluation_ , Bamberger et al. (2006) identify recall as one of the methods available for reconstructing baseline data ―...to

> 2 For example, while there has been a substantial growth in impact evaluations of the World Bank development projects, only 8.8% of World Bank investment loans in 2009/10 had an impact evaluation. In 1999/00 the proportion was 2.4%. 3

> This arises from the externalities in evaluation, given that main support for the evaluation typically comes from the manager of that specific project, while benefits accrue more broadly. This leads to under-investment in evaluations generally but especially long-term evaluations, as are crucial for certain types of development projects. These issues are discussed further in Ravallion (2009).

> 4 On the strengths and weaknesses of such designs see Featherman (1908), Janson (1990) and Solga (2001).

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obtain estimates of major changes in the welfare conditions of the household‖ (p.98) and they provide examples.<sup>5</sup> They offer a cautiously positive assessment of this method: ―Recall is a potentially valuable, although somewhat treacherous, method to retroactively estimate conditions prior to the start of the project and hence to reconstruct or strengthen the baseline data. Although the literature on the reliability of recall is quite limited, particularly in developing countries, available evidence suggests that although information from recall is frequently biased, the direction, and sometimes magnitude, of the bias is often predictable...so that usable estimates can often be obtained.‖ (Bamberger et al., 2006, p.98.) How confident can we be about the potential for using retrospective recall of outcome changes as a proxy for the actual changes in an impact evaluation?<sup>6</sup> Some observers have argued that long-term recall of changes in the overall standard of living provides a usable signal. For example, Narayan, Pritchett and Kapoor (2008) use a 10 year recall period for changes in living standards in studying poverty dynamics in developing countries. Krishna (2004) and Krishna et al. (2006) use a 25 year recall period for essentially the same purpose. There have been very few tests of long recall, but in one of the few examples, Berney and Blane (1997) found evidence that 50 year (!) recall of relatively simple information (father’s occupation, type of dwelling, number of rooms, water and sanitation facilities) was quite reliable in a small sample of British adults.

Yet the literature is also replete with warnings on how unreliable retrospective studies can be, given the limitations of human memory. ―Telescoping‖ is thought to be common, whereby important events are remembered reasonably well but placed at the wrong time; errors of both omission and commission also occur.<sup>7</sup> Recall of precise quantities, such as food consumed, is unlikely to be reliable over more than a month or so. A degree of recall failure is to be expected although it should not be presumed that longer recall periods necessarily give less accurate answers. That depends on what one is asking about. Longer term recall of changes in overall standard of living may well be more reliable than for (say) quantities of food consumed.

However, the issue here is not whether people can recall well how they lived 10 years ago (say), but rather whether such data is reliable for inferring the impacts of an intervention in

> 5 Also see Broegaard et al. (2011). Retrospective recall of baseline information has also been used in evaluative medical research. See, for example, Watson et al. (2007) and McPhail and Haines (2010).

> 6 One might argue that recall of changes in subjective welfare is of intrinsic interest, even if it does not accord well with reality. For example, this is argued by Narayan et al. (2008, p.8). That may well be, but here it is assumed that one is only interested in recall as a proxy for missing data on outcomes, for the purpose of an impact evaluation where there is an objective outcome measure appropriate to the specific project.

> 7 Janson (1990) reviews the evidence on recall errors. For useful overviews of these and other issues in survey design also see Fowler (1995) and Iarossi (2006).

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the absence of baseline data. In past applications of long-term recall, the precise period of time is not so important. In an impact evaluation, telescoping could be a more serious concern since one wants to know welfare changes since the precise time the project started. The reliability of recall will then depend on the time profile of benefits from the specific project. Given the scope for telescoping, it will clearly make a difference whether those benefits are evenly spread over time or concentrated in some sub-period.

There is another reason why we might be concerned about the reliability of this shoestring method. The questions asked are likely to be subjective-qualitative; indeed this is recommended practice, on the presumption that recall of quantitative data is unreliable (Bamberger et al., 2006). Such methods can also reduce the cost of the evaluation; development outcomes such as consumption or income require relatively complex and costly surveys. However, the literature on subjective welfare (―well-being‖) points to concerns about this type of data, especially when used as a dependent variable, as here. If we could assume that the errors are white noise then they will not create bias, although they may make it harder to obtain precise estimates of impacts. However, there are reasons to expect systematic effects. The fact that these are typically subjective data on outcomes suggests that non-ignorable measurement errors and personality/mood effects on self-assessed welfare will be present, and there are good reasons to expect the errors in subjective data to be correlated with other explanatory variables (Bertrand and Mullainathan, 2001; Ravallion and Lokshin, 2001).

There is also the possibility that the intervention may alter the scales used in subjective questions—such as what it means to be ―poor‖ or ―very satisfied‖ with life—thus biasing the results even with perfect recall. People will naturally interpret the scales used in a subjective question on welfare relative to their personal knowledge and experience, which might well be influenced by the intervention. There is evidence of systematic effects of respondent characteristics on how scales are interpreted in subjective questions (Beegle et al., 2012).

The upshot of these observations is that subjective responses on outcomes must be expected to contain statistically non-ignorable noise for the purposes of an impact evaluation.<sup>8</sup> If

> 8 This is well recognized in the literature on using subjective welfare data in economics, where the focus is on the regression function of subjective welfare on covariates rather than the actual values reported by respondents. For an overview of the literature see Ravallion (2012).

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program placement was random and impacts common across all units then one would not be concerned, although heterogeneous impacts cloud the picture, even in an experiment.<sup>9</sup> In nonexperimental evaluations, biases can be expected even under homogeneous impacts.

However, the literature on policy or program evaluation does not contain (to my knowledge) even a single example in which this type of baseline recall has been tested against conventional survey data collected at both the baseline and post-intervention.

This paper tries to help fill this gap in our knowledge. The paper reports on an experiment that was designed to test the idea of using retrospective data as a substitute for baseline data from a contemporaneous survey. After collecting baseline and post-intervention data for treatment and comparison units to allow estimation of a standard double-difference (DD), a series of recall questions were asked on how various dimensions of welfare had changed since the time the project was introduced. This allows what I will call the ―shoestring double difference‖ (SDD) estimator. More precisely, the two estimators of mean impacts are:

> Here  _Yi_  _Yi_ 1  _Yi_ 0 is the measured change in consumption between the baseline (date 0) and post-intervention surveys (date 1) for the respondent in household _i_ , where each respondent is assigned to either the treatment (the set _T_ ) or comparison group ( _C_ ), and<sup>_R_</sup> _i_<sup>denotes the</sup> subjective recall of the change in living standards over the same period.

Two versions of the SDD estimator are studied here: SDD1: This assumes that no baseline data are available. Only an ex-post survey can be done. Thus no adjustments are made for selection bias based on contemporaneously observed pre-intervention differences that might influence subsequent trajectories.

> 9 For example, suppose that the true impacts of a project are greater for poor people, for whom recall is less reliable. (There is supportive evidence for this conjecture in Das et al., 2011, who found health-status recall to be worse for poor people, using data for India.) Then we will obtain a biased estimate of the difference in impacts between poor and non-poor people even with randomized assignment of the intervention.

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SDD2: This assumes that only the data on outcomes are missing. Thus standard corrections can be made for selection bias based on other observables at the baseline.

Note that the difference is in whether an allowance is made for selection on observables. If the recall of changes since the introduction of the project works well then both SDD1 and SDD2 will be able to address selection based on (time-invariant) unobserved factors.<sup>10</sup> Importantly, the shoestring evaluations were ―tacked onto‖ a full scale evaluation. This was for a large antipoverty program in poor areas of rural China, and the results are reported in Ravallion and Chen (2005) and Chen, Mu and Ravallion (2009). The paper is thus able to compare SDD1 and SDD2 to the ―actual‖ DD, as estimated from high-quality, comprehensive and contemporaneous baseline and follow-up surveys. The implications for the structure of recall errors are also examined.

The findings from this case study suggest that SDD methods are vulnerable to biases that confound identification. Respondents’ perceptions of how their living standards have changed provide a weak and biased signal of consumption changes measured from contemporaneous surveys. There are also signs of ―false positives‖ stemming from the weak ability of retrospective recall of welfare changes to neutralize selection bias based on unobserved initial conditions influencing program placement.

The following section describes the project and data. Section 3 presents the impact estimates, while section 4 explores the responses on recall further to help understand the results in section 3. Section 5 concludes.

# **2. Setting, data and methods**

The project being evaluated is the World Bank’s Southwest China Poverty Reduction Project—the Southwest Program (SWP) for short. This comprised a package of multi-sectoral interventions targeted to poor villages using community-based participant and activity selection. The aim was to achieve a large and sustainable reduction in poverty. The project was implemented in selected poor villages in the designated poor counties of Guangxi, Guizhou and

> 10 On the distinction between selection bias based on observables and that based on unobserved factors see Heckman et al. (1998).

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Yunnan. The total investment per capita under the SWP was roughly equal to mean annual income per capita of the project villages.

Within the selected villages, virtually all households were expected to benefit from the infrastructure investments under SWP, such as improved rural roads, power lines and piped water supply. Widespread benefits were also expected from the improved social services, including upgrading village schools and health clinics, and training of teachers and village health-care workers. Those with school-aged children also received tuition subsidies as long as the children stayed in school. Over half of the households in SWP villages also received individual loans at a lower interest rate than for commercial sources of credit. The loans financed various activities including initiatives for raising farm yields, animal husbandry and tree planting. There was also a component for off-farm employment, including voluntary labor mobility to urban areas and support for village enterprises. The selection of project activities aimed to take account of local conditions and the expressed preferences of participants.

Chen, Mu and Ravallion (2009) report results from an intensive survey data collection effort over 1995-2005 spanning both treatment and comparison villages.<sup>11</sup> All surveys were implemented by the Rural Household Survey (RHS) team of the government’s National Bureau of Statistics (NBS). The baseline survey covered 2,000 randomly-sampled households in 200 villages, with roughly half not participating in the SWP. A final post-intervention survey was done in 2004/05. Surveys were also done during the disbursement period up to its end, in 2000.

There are 112 SWP villages and 86 non-SWP villages in the sample. The SWP villages were a random sample from all project villages, while the non-SWP villages were a random sample from all other villages in the designated poor counties. Ten randomly sampled households were interviewed in each village.

The surveys included community, household and individual questionnaires. The community schedule collected data on natural conditions, infrastructure and access to services. The household survey collected data on ( _inter alia_ ) incomes, consumptions and assets. The individual questionnaires covered gender, age, education and occupation.

> 11 The attrition rate was 12% over the full period. Chen et al. discuss tests for attrition bias and for bias in selecting replacement sample households.

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Relative to other household surveys, unusual effort went into obtaining accurate data on consumption and income. While the community, individual and project activity surveys used conventional one-time interviews each year, the household surveys were quite different. The surveys were closely modeled on NBS’s Rural Household Survey (RHS) (which is described in detail in Chen and Ravallion, 1996). This is a good quality budget and income survey, notable in the care that goes into reducing both sampling and non-sampling errors. Similarly to the RHS, sampled households maintain a daily record on all transactions plus log books on production. Local interviewing assistants visited each household at two-three weekly intervals to monitor compliance and check questionable data entries or inconsistencies found at the local (countylevel) NBS office. Other trained interviewers also visited at regular intervals to collect additional data. This intensive interviewing method is in marked contrast to most surveys in which the respondent is visited only once or twice.

The consumption aggregate was built up from very detailed data on cash spending on all commodities and imputed values of consumption from own household production, valued at local selling prices. Living expenditures exclude spending on production inputs (which are accounted for in net income from own-production activities).<sup>12</sup> The income aggregate includes cash income from all sources and imputed values for in-kind income. Income is measured net of all production costs, including interest on debt (including loans from the SWP). The outmigrating workers were not tracked, although the income aggregate includes remittances received from family members who migrated, including those supported by the SWP. Remittances are expected to be the main means by which the out-migration component reduced poverty in the short run.

For the 2004/05 follow-up survey, exactly the same survey instrument was used as for the prior surveys. However, toward the end of the period, a rapid-appraisal module was designed by the author and refined based on field testing. The Chinese and local language versions of the module were refined on the basis of field tests in poor villages in a number of locations.<sup>13</sup> For the

> 12 Living expenditures exclude transfer payments, although these only account for a small share of total spending (3.7% over the whole sample in 1996).

> 13 In the development stage for the module, the first field testing was done over two days in two selected poor villages in Jiangxi, and then revised. The module was then fields in 12 villages in Jiangxi, and further refined. The Jiangxi work was supervised by Solveig Buhl (GTZ staff member assigned to the provincial poor-area program

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purpose of the present paper, in 2005 the module was added to the final survey of treatment and comparison samples in the SWP evaluation to elicit perceptions of how welfare had changed over time since the project began. The module asked respondents to assess whether various aspects of their lives had improved over the preceding 10 years. These involved a long list of aspects of well-being and in each case the respondent was asked whether this item had improved or not over the last 10 years, on a 5-point scale, ―much worse,‖ ―slightly worse,‖ ―no different,‖ ―slightly better‖ and ―much better‖. Matching questions were asked about perceived current standards of living. The sample was restricted to adults who were at least 28 years of age at the time of the interview.

In measuring impacts for such a program one should allow for bias arising from how differences in initial characteristics influence subsequent trajectories; this is known to be important in poor-area development projects.<sup>14</sup> Chen et al. (2009) used propensity score (PS) weighting and trimming for this purpose. The method proposed by Hirano, Imbens and Ridder (2003) was used for PS weighting.<sup>15</sup> This allows for heterogeneity in the (observable) baseline characteristics that may be correlated with subsequent changes over time and so bias the DD results. The samples were also trimmed to assure sufficient overlap in propensity scores.<sup>16</sup> Of course, these adjustments for bias require the baseline data. Only the results without PS weighting and trimming would be feasible in a single survey round post-intervention.

In estimating the probits for whether a village was selected for SWP, covariates were chosen to reflect the selection criteria used by the project staff as well as the research team’s priors on how other factors (such as remoteness and village ethnicity) may have influenced SWP placement. Chen et al. (2009) discuss the results in greater detail. They found that project villages tended to be in more hilly/mountainous areas, less well endowed with infrastructure, with lower mean income and consumption in the baseline. In most respects, the SWP villages tended to be poorer than other villages within the project counties. Using the propensity scores

> office). The module was further tested and refined by staff of the national and provincial statistics offices in each of the three study provinces.

> 14

> Jalan and Ravallion (1998) provide evidence using regional growth models for rural China.

> 15 For details see Chen et al., (2009).

> 16

> For their ―trimmed sample‖ Chen et al. (2009) chose the PS interval (0.1, 0.9), corresponding to the efficiency bounds recommended by Crump et al. (2006) for estimating average treatment effects with minimum variance.

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based on the probit to re-weight the data, Chen et al. (2009) were able to obtain a close balancing of the characteristics of the two samples (including in the means of the initial outcome variables), particularly after trimming the samples.

Note that these adjustments for selection bias are based on observable differences in the baseline. That still leaves any bias due to unobserved factors with time varying effects. Only selection bias due to (additive) time-invariant unobserved factors is removed using the time differencing component of the DD.

# **3. Impact estimates**

Table 1 summarizes the findings from the full impact evaluation as reported in Chen et al. (2009). The table gives DD estimates of the impacts of SWP on consumption and income for both the full sample and the sample trimmed for common support and using PS weighting.

There is little or no impact of the SWP on consumption or income over the full period. This holds using a standard DD estimator as well as the PS weighted estimator on the trimmed sample. The table also includes impact estimates for 2000, at the end of the SWP’s disbursement period. Interestingly, we see a significant impact on incomes during the disbursement period, but evidently this was all saved (as discussed further in Ravallion and Chen, 2005). However, there is little sign of longer-term impact.<sup>17</sup> Given this uneven spread of the impacts of SWP—concentrated in the earlier half of the study period—telescoping could well be a problem in using recall. The reliability of the SDD method will depend critically on the ability of respondents to recall the income gains over five years ago, and correctly identify those gains as being within the last 10 years.

Table 2 summarizes the findings from asking in 2005 whether various aspects of wellbeing had improved over the previous 10 years. (This is a complete listing of results for all the recall questions asked.) The first main column of the table gives the SDD1 estimator, which is the single difference between SWP villages and non-SWP villages in the proportion of the

> 17 Chen et al. (2009) also study the heterogeneity in impacts and find that SWP could have had substantially higher overall welfare impacts if it had been targeted differently. They also study spillover effects of the program, given behavioral responses of local governments.

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population saying that the item in question had ―obviously improved‖ or better.<sup>18</sup> Note that since the question already embodies the change over time, the single difference can be interpreted as a double-difference estimate of the impact on the underlying level of that variable.

The subjective assessments by SWP participants of whether their living standards had improved since the project began are not significantly different to those found for the non-SWP villages. For example, 36% of those in the SWP villages reported that their overall standard of living had ―obviously improved‖ over the last 10 years. But this was also true of 36% of those in the non-SWP villages, implying zero impact of the project.

Ostensibly these SDD1 results are consistent with the findings reported in Chen et al. (2009) indicating little or no long-term impact of the SWP on consumption (or income). However, a closer inspection leads one to question how much comfort one can get from this finding, from the point of view of assessing the scope for using SDD. There is in fact very little correlation between the perceived changes in standard of living and the changes in log consumption per person between 1996 and 2004/05; the correlation coefficient is 0.09 for SWP villages, which is only significant at the 8% level (t=1.78); in the non-SWP villages, the correlation is even lower at 0.01. So the fact that SDD1 accords well with the DD estimator using actual consumptions is not because subjective welfare is revealing well the changes in consumption measured in the baseline and follow-up surveys. SDD1 would also show no impact if the recall data was a pure white noise error process.

When we turn to the SDD2 estimator—incorporating an allowance for selection bias on observables—we start to see signs of impact on overall living standards (Table 2). There is also a sign of impact on perceptions of living standards in the village as a whole. Possibly these signs of impacts are statistical flukes; with 30 outcome variables, one could easily get one or two significant effects by pure chance. However, looking at the entire column of differences between outcomes in treatment and comparison villages in Table 2 it is notable how much more positive they are (although often not significantly so) using SDD2. There appears to be something else going on here. The rest of this paper will try to figure out what it might be.

> 18 I also tested sensitivity to using both a lower and higher cut-off; in neither case did I find any significant difference between SWP villages and the comparison villages.

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It might be conjectured that the signs of positive welfare impacts using SDD2 reflect some broader concept of ―welfare‖ than captured by consumption. Or one might argue that welfare recall uses different implicit weights, possibly reflecting missing or imperfect markets. Looking at the SDD2 results in Table 2, there is some sign of an impact on ―health‖ that may account for the implied gain in overall standard of living. Amongst the consumption goods, clothing shows the strongest positive impact using SDD2. However, there is less sign of impacts on any of the many other dimensions of welfare for which the recall questions were used. Nor is it clear why these effects would only emerge when one uses the SDD2 method.

As an additional test for differences between project and comparison villages in ―nonincome‖ factors in subjective welfare I exploited the fact that the recall module included questions on perceived current living conditions (for the same items in Table 2). I examined the relationship between the answers for overall standard of living and consumption per person in the 2004/05 survey data, to see if there are any signs that the relationship is different between SWP and non-SWP villages, as might arise from impacts of SWP on ―non-income‖ dimensions of welfare captured in the subjective assessments. The test entailed regressing each subjective measure of the level of welfare on log consumption per capita in 2004/05, a dummy variable for SWP villages and the interaction effect between these two variables. There were no significant differences between SWP and non-SWP villages for all except one of the categories in Table 2. The one exception was for roads (―are you satisfied with village road conditions?‖); households with higher consumption in the SWP villages tended to rate road quality higher, but there was no such gradient in non-SWP villages. One might take this to suggest that the SWP enhanced perceived road quality for better-off households, although one cannot dismiss the possibility that one will get at least one significant result in 30 tests purely by chance.

These observations are hardly conclusive, but they don’t leave one confident that SDD2 has revealed some genuine impacts that were somehow missing from the DD and SDD1 estimates. As the next section will show, a further insight into the SDD estimates can be obtained by looking more closely at the relationship between the recall of changes in household living standards since the project began and the measured changes in consumption.

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# **4. Relationship between the impact estimators**

To better understand the relationship between the two estimators, I postulate the following regression models for the recall responses: Here _X_ is a vector of controls and _k i_<sup></sup> _i_<sup>(</sup><sup>_k_=</sup><sup>_T_,</sup><sup>_C_) are error terms. Notice that all parameters can</sup> vary according to whether the treatment is received or not. So this specification allows for the possibility that the two groups have different perceived changes in welfare at given ( _Yi_ 1, _Yi_ 0, _X i_ ). _k_ In estimating (2) it will be assumed that _E_ (<sup></sup> _i Yi_ 1, _Yi_ 0, _X i_ , _i_  _k_ )  0 ( _k_ = _T,C_ ) (as required for OLS to be unbiased). This can be questioned. For example, there may well be omitted variables influencing recall on how living standards have changed and correlated with _Yi_ 1, _Yi_ 0, _X i_ .

Table 3 gives the estimates of (2). The dependent variable takes the value 1 if the overall standard of living is deemed to have ―obviously improved‖ or better, and zero otherwise. I use the full samples (without trimming for common support) and the _X_ vector comprises gender, age and age squared.

Recall that the answers on retrospective recall of changes in overall living standards were essentially orthogonal to the contemporaneously measured changes in consumption. With the controls, significant partial correlations emerge, for both treatment and comparison villages (Table 3). There is also a significant (positive) effect of baseline consumption after controlling for the measured change in actual consumption. This is suggestive of a systematic economic effect on recall errors. Comparing two households with the same actual consumption gain, the poorer one is less likely to report that its standard of living has improved based on recall. There are also signs of gender and age effects. However, the R<sup>2</sup> ’s are low; over 95% of the variance in recall of changes in the household’s overall standard of living is left unexplained.

Of course, what matters for the impact evaluation is the difference between the models _T C_  for the treatment and comparison groups. If  1  1 then (2) implies a linear relationship 13
between SDD and DD. And this is supported by the data. One cannot reject the null hypothesis _T C_ that  1   1   1 . Using equations (1) and (2) we then see obtain SDD as the following linear function of DD: We can now identify three distinct reasons why SDD is a poor proxy for DD. First, other factors influence SDD besides DD (equation 3). Their weight depends on how similar the treatment and comparison groups are in terms of the means of initial consumption, other covariates and in the model parameters. Table 3 suggests that the (positive) effect of baseline consumption on the perceived change in living standards (after controlling for the measured change in actual consumption) is stronger for the comparison group, which also had higher mean consumption given the selection process. (This suggests that, without matching or trimming,  0 _T E_ ( _Yi_ 0 _i_  _T_ )  0 _C E_ ( _Yi_ 0 _i_  _C_ )  0 .) Thus SDD1 is unlikely to perform well, since one would not have the baseline data on covariates of outcomes needed for matching. Essentially, the selection bias adds noise in the relationship between DD and SDD. But even SDD2 may perform poorly as an indicator of DD since in practice one probably cannot balance initial outcomes.

Second, even for the classic case of a randomly assigned program with common _T C_ impact—for which we could justify setting  0 _E_ ( _Yi_ 0 _i_  _T_ )   0 _E_ ( _Yi_ 0 _i_  _C_ ) and _T C_  _E_ ( _X i i_  _T_ )  _E_ ( _X i i_  _C_ ) ) in equation (3)—the coefficient on DD (  1 ) of around 0.3 implies that a very large impact on consumption would be needed to switch the recall variable from zero to unity. Indeed, consumption would need to increase about 30 fold (e<sup>1/0.3</sup> is about 30)! Clearly SDD is a blunt indicator for DD.

Third, a further observation on Table 3 is that the coefficients on the change in log consumption and 1996 log consumption are very similar; indeed, one cannot reject the null _k k_ hypothesis that they are the same (  1   0 for _k=T,C_ ), although the restriction performs less well for the comparison group. Under this null, it is current consumption that is driving perceptions of past welfare gains. This can be interpreted as ―telescoping,‖ although for the treatment group the recall of changes in the standard of living appears to put too little weight on 14
baseline consumption, while for the comparison group the weight is too high. (Again this probably reflects the selection into the program.) Thus, equation (3) becomes: This is the lethal blow to SDD: it ceases to have any value as an indicator of DD if there is any selection bias, generating baseline differences in consumption.

_k k_  In the light of these findings, let us return to the results in Table 2. Given that  1  0 , using recall of welfare changes since the baseline essentially amounts to ignoring the baseline differences. So (roughly speaking) one is regressing (subjectively-assessed) final welfare outcomes (plus the noise in subjective responses) on treatment status. The error term in the SDD1 estimator will contain the selection bias based on both observed and unobserved factors, whether time varying or not.

What then is SDD2 giving us? Adjusting the SDD estimate using PS weighting and trimming aims to balance the treatment and comparison groups in terms of baseline covariates. This provides some protection against selection bias based on observables. But the heavier contamination by selection bias due to unobserved factors in the recall data may well be working in the opposite direction to the selection bias based on observables. The impact found using SDD2 could then be picking up some latent factor in subjective welfare that also helped facilitate village participation in the SWP. In this case study, it is safe to assume that SDD2 has largely removed the effects of the readily observable targeting criteria used to assign villages to the SWP. However, there are clearly unobserved factors, such as the influence of local political operatives. And these could well be correlated with subjective welfare levels in the village. So the ability of the DD estimator to eliminate the unobserved factors in selection is key to credibly estimating the impact. And (by the same logic) the evident inability of the SDD to do so makes it vulnerable to bias.

By this interpretation, given the structure of the errors in recall, eliminating selection bias based on observables, SDD2 is revealing the remaining selection bias based on unobservables that is found in the recall responses on welfare changes.

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# **5. Conclusions**

Given that it is rare to evaluate development projects by repeated observation over a long period, this case study has provided an opportunity to study a less costly method, based on respondent recall using subjective-qualitative questions. Success for this method would open up many low-cost opportunities for learning about development effectiveness.

Neither the ―expensive‖ nor ―shoestring‖ double-difference estimates suggest that the poor-area development program studied here had a significant long-term impact on living standards in poor areas of rural China. But their agreement is not because the retrospective qualitative assessments provided good proxies for the changes in consumption derived from high-quality contemporaneous surveys. Indeed, the analysis suggests that long-term recall of the household’s overall standard of living contains only a weak and biased signal of changes in consumption. Controlling for the actual change in consumption, the recalled improvement in living standards tends to be higher for initially richer households. There are clear signs of telescoping in the recall responses, but the bulk of the benefits occurred in the earlier half of the recall period, which is given too little weight by respondents in treatment villages. Recall is clearly also affected by many idiosyncratic factors not accountable to consumption.

Furthermore, there is an indication that the shoestring method can be deceptive. By not being able to effectively address the problem of selection bias based on the unobserved factors that determined which villages got selected for the program, the recall method becomes vulnerable to spurious impact signals. In this particular case, the recall method suggests positive impacts after controlling for observed differences between treatment and comparison villages at the baseline. The paper has argued that a plausible interpretation of this finding is that the selection bias based on observables is working in the opposite direction to that based on unobserved factors. Thus, only reducing the former bias (by balancing the distribution of observables between treated and comparison units) makes matters worse.

So (alas) this case study does not offer much encouragement on the reliability of this ―shoestring approach.‖ Of course, this is just one study, and the only one to date in the context of policy or program impact evaluation. Further tests are needed. Thankfully, the marginal cost of doing such tests in the context of a full-scale evaluation is not high.

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