The Effect of Non-Contributory Pensions on Labour Supply and Private Income Transfers: Evidence from Singapore

Non-contributory pensions are becoming increasingly prevalent worldwide. As their effects are likely to be context-dependent, evaluating their effects in a wide range of settings is important for establishing the external validity of the non-contributory pension literature. We use a new monthly panel dataset and a difference-in-differences strategy to study the effect of a new non-contributory pension in Singapore (the Silver Support Scheme, or SSS) on labour supply, work expectations, private cash transfers, and expenditure, one year after its implementation. We find no evidence that receiving SSS payouts led to a fall in labour supply, work expectations, or the receipt of private cash transfers in the first year after SSS implementation – our estimated effects for these outcomes are statistically insignificant, and are either negative but close to zero, or positive. Our point estimates of the effects of receiving SSS payouts on expenditure are positive but too imprecise to allow us to make any definitive conclusions. Lastly, we do not find evidence of anticipatory effects among younger individuals who are not age-eligible for payouts yet. These results, when coupled with our finding in a companion paper that the SSS improved recipients’ subjective well-being (Chen & Tan, 2017), suggest that the SSS was successful in improving recipients’ welfare without substantial crowding out of private transfers or changes in labour market behaviour of current and future SSS beneficiaries.


Introduction
Non-contributory pensions are becoming increasingly prevalent worldwide (International Labour Office, 2014). These pensions play a crucial role in improving the retirement security of individuals who do not receive sufficient benefits from contributory pension schemes (e.g. lowerincome workers, informal sector workers, or housewives), but can have potentially large effects on labour markets and household dynamics. The importance and increasing prevalence of noncontributory pensions has led to a growing body of research that evaluates their impact on key outcomes such as labour decisions, intra-family cash transfers, and expenditure (see e.g. Case & Deaton, 1998;Fan, 2010;Amuedo-Dorantes & Juarez, 2015;Bando et al., 2016;Galiani et al., 2016). However, the effect of non-contributory pensions can vary across countries due to differences in institutions, social norms, and benefit levels. It thus remains important to evaluate each new or reformed non-contributory pension, to improve the external validity of the literature as a whole 1 .
In this paper, we evaluate the effects of Singapore's first national non-contributory pension (the Silver Support Scheme, or SSS) on labour decisions, cash transfers among family and friends, and expenditure, one year after its implementation. The SSS is a means-tested scheme that targets the neediest 20 -30% of Singaporean citizens aged 65 and above. It was announced in end-March 2016 with details on the exact qualifying criteria and payout levels. The first payout was disbursed in end-July 2016. Payouts are disbursed on a quarterly basis, and on average, recipients of SSS payouts in our sample receive around S$500 per quarter, which corresponds to about 14% of the pre-SSS-announcement mean monthly income from work among SSS recipients who worked during that period. Eligibility for the SSS is automatically determined based on government administrative data and updated yearly. Disbursement of payouts is equally automatic and fussfree, as it is processed through well-established distribution channels.
We use a difference-in-differences (DiD) strategy to identify the causal effects of the SSS.
The sample for our main analysis is made up of individuals aged 65 and above in 2016 2 . The treated group consists of those who reported receiving an SSS payout at least once in 2016, while the control group consists of those who did not. Our treatment definition allows us to interpret the policy shock as exogenous, since eligibility of payouts for 2016 was based on 2015 administrative data. Individuals were thus unable to select into treatment after the SSS was announced in March 2016. To tackle the possibility that our treatment and control groups may be sufficiently different to invalidate the DiD parallel trends assumption, we trim our sample, using individuals' treatment propensity, to construct more similar treatment and control groups. We also verify that our results are robust to a battery of checks that include the use of different control groups, different reweighting techniques, and the addition of group-specific time fixed effects (details in Section 5).
Our data comes from the Singapore Life Panel (SLP), a new longitudinal monthly survey, which aims to follow a population-representative sample of Singapore citizens and permanent residents aged 50 -70 and their spouses. (See Vaithianathan et al. (2017) for more details on the SLP.) It captures a rich set of data including demographic characteristics, labour decisions, private cash transfers, and expenditure. Its monthly responses allow us to precisely account for announcement effects, to avoid under-estimating the SSS's effects (see, e.g., Blundell et al., 2011 for evidence on the importance of accounting for announcement effects). 2 We also carry out a supplementary analysis on the effects of expecting to receive the SSS on younger individuals who are not age-eligible for payouts yet (i.e. individuals aged 56 -63 in 2016). For clarity of our exposition, this supplementary analysis is discussed in more detail only in Section 7. All other sections describe our main analysis on the effect of receiving SSS payouts, using a sample of individuals who can already start to receive payouts, i.e. aged 65 and above in 2016. improving recipients' welfare without substantial crowding out of private transfers, reductions in labour supply, or changes in the behaviour of younger individuals who expect to receive SSS payouts in future.
Apart from evaluating an important new pension reform in Singapore, our paper contributes to the literature on the effects of non-contributory pensions on the labour market. In our paper, the estimated effect of the SSS on participation in paid work is lower (close to zero, and statistically insignificant) than the fall of 4 to 6 percentage points that many other studies on non-contributory pensions find (Aguila et al., 2011;Hernani-Limarino & Mena, 2015;Juárez & Pfutze, 2015;Bando et al., 2016;Cheng et al., 2016;Fetter & Lockwood, 2016;Galiani et al., 2016) 6 . Interestingly, Galiani et al. (2016) and Bando et al. (2016) find no effects on overall labour supply about one year after a non-contributory pension was rolled out in Mexico and Peru respectively, as there was a shift from paid work to unpaid work. Galiani et al. (2016) explain that the shift could be due to beneficiaries preferring "less stressful and less demanding informal unpaid work within the household". Following this line of argument, it is possible that we do not see a drop in paid work participation because paid work in Singapore could be less stressful and demanding than that in the developing countries, and little informal unpaid work within the household (such as farming and handicrafts) is available in Singapore. The lack of an effect on the intensive margin may also be partially explained by labour market constraints on minimum working hours (see e.g. Stewart & Swaffield, 1997;Euwals, 2001;Martinez-Granado, 2005 for evidence on constraints on working hours). In addition, the relatively small quantum of SSS payouts (in relation to both recipients' wage and payouts from many other non-contributory pensions) 7 , as well as the possibility that 6 Some have found bigger effects (e.g. Danzer, 2013;Juárez & Pfutze, 2015). 7 The average SSS payout in our sample is about 14% of the pre-announcement mean monthly wage among SSS recipients who worked, substantially lower than payouts from many other non-contributory pensions studied in the literature. E.g., payouts were equivalent to more than twice the median per capita income in South Africa (Case & work behaviour may take time to change, may also explain our result. Regardless of the exact reasons for the smaller estimated effects in our sample, our results suggest that the effects of noncontributory pensions on labour supply, as well as the speed of labour market adjustment, are likely to vary by payout level and/or institutional context. Our results also add to the literature on whether private cash transfers are crowded out by public transfers. Findings from this literature are more disparate; effects can range from complete crowding out to little response, though many studies suggest that increasing public transfers by a dollar leads to a 20 -30 cent fall in private transfers (Cox & Fafchamps, 2008). In the specific context of non-contributory old age pensions, Koh and Yang (2017) find that a new old-age pension in South Korea completely crowded out money transfers from adult children to parents. Jensen (2004) and Fan (2010) find that expansion or the introduction of new non-contributory pensions led to falls in private cash transfers equivalent to 25% -30% (for South Africa) and 30% -39% (for Taiwan) of the payout quantum respectively. Bando et al. (2016) and Amuedo-Dorantes and Juarez (2015) estimate that the probability of receiving a private transfer dropped by 7-8 percentage points respectively in Peru and Mexico respectively about one year after the implementation of a non-contributory pension for the elderly. On the other hand, Hernani-Limarino and Mena (2015), Behrman et al. (2011), andCheng et al. (2016) find little evidence that the introduction or expansion of non-contributory old age pensions in Bolivia, Chile, and China had an effect on receipt of private transfers. Against this backdrop, our finding that SSS recipients do not appear to receive less private transfers may not be surprising. Our result could be driven by a few reasons. The exchange motive could be stronger than the altruistic motive for private Deaton, 1998;Jensen, 2004), 96% and 76% of mean labour income for eligible individuals in Mexico (Juárez & Pfutze, 2015;Galiani et al., 2016) and Peru  respectively, and about 25% of the 1939 median wage for 60-64 year olds for the US's Old Age Assistance program (Fetter & Lockwood, 2016). transfers (see e.g. Cox, 1987;Cox & Jakubson, 1995), as it is common for grandparents in Singapore to provide care for their grandchildren. The SSS payout quantum could also be small enough for "donors" of private transfers to brush off 8 , and lastly, donors' behaviour may also take time to adjust. In all, our results for labour decisions and private transfers suggest that the effects of non-contributory pensions are likely to vary by institutional context and payout levels.
The rest of this paper proceeds as follows. Section 2 provides background information on SSS. Section 3 describes our data and construction of the key treatment variable. Section 4 elaborates on our identification strategy and main empirical specifications, while Section 5 describes our alternative specifications for robustness checks. Section 6 presents our results.
Section 7 discusses our supplementary analysis on the anticipatory effects of the SSS on younger individuals who are not age-eligible for payouts yet. Note that Sections 2 -6 focus only on the main analysis, which looks at the effect of receiving SSS payouts among those who can already start to receive payouts, i.e. those aged 65 and above in 2016. Lastly, Section 8 concludes.

Background on the Silver Support Scheme 9
The Silver Support Scheme (SSS) is the first non-contributory pension implemented in Singapore, and is targeted at the neediest 20 -30% of Singaporean citizens aged 65 and above.
The introduction of SSS is a significant turning point in Singapore's pension system, which has been dominated by a defined contribution scheme, the Central Provident Fund. 8 E.g., SSS recipients in our sample receive payouts equivalent to about 14% of their mean pre-announcement wage. This is substantially lower than, e.g., the 76% of mean per-adult-equivalent labour income that recipients in 's study receive. 9 Most of the details in this section can also be found in our companion paper which looks at the effect of the SSS on subjective well-being (Chen & Tan, 2017). SSS details, such as the exact eligibility criteria and payout amounts, were announced at the end of March 2016 10 . Eligible individuals receive quarterly payouts of S$300 -S$750 to supplement their existing retirement income; the exact quantum depends on the type of public housing (HDB) flat they live in 11 . Singaporeans who live in smaller flats will receive more as the government uses flat-type as a proxy for socioeconomic status. On average, recipients of SSS payouts in our sample receive around S$500 per quarter, which corresponds to about 14% of the pre-SSS-announcement mean monthly income from work among SSS recipients who worked during that period in our sample. The first payout was made in end-July 2016, followed by end- Individuals' eligibility for SSS is automatically determined based on administrative data, and is updated yearly. Eligible individuals must (i) be Singapore citizens; (ii) live in a 1-to 5-room HDB flat; (iii) not personally own or have a spouse who owns 5-room or larger HDB flats, private property, or multiple properties; (iv) have contributed no more than S$70,000 to their defined contribution accounts by age 55; and (v) have a household per-capita income of S$1,100 or below.
Self-employed persons should also have an average annual net trade income of not more than $22,800 when they were between the ages of 45 and 54. Since the eligibility for the 2016 payouts is based on government data available in 2015, the receipt of SSS payouts in end-July and end-10 The Government first announced the introduction of the Silver Support Scheme (SSS) in August 2014, but details on qualifying criteria were not announced then. This implies that even if Singaporeans had some expectations about whether they would receive payouts from SSS, these expectations were probably weak. 11 80% of Singaporeans (as of 2016see Department of Statistics (2017)) live in public housing apartments (flats) which come in different sizes, and 90% of these households own their flat (Housing and Development Board, 2017). Flat sizes or flat-types are often used as a proxy for socio-economic status by the government to target subsidies and transfers. The SSS payout quantum schedule for individuals living in each type of flat is: 1-and 2-room flats: S$750; 3-room flats: S$600; 4-room flats: S$450; 5-room flats: S$300.
September 2016 is pre-determined and hence exogenous. However, individuals may be able to self-select into being eligible for SSS payouts in 2017 by moving into a smaller flat, or by reducing their income. We discuss how we deal with this issue in Sections 3.2 and 4 12 .
The disbursement of SSS payouts is fuss-free for recipients, as the Singapore government has been giving out ad-hoc or regular cash transfers to Singaporeans since (at least) 2008, and thus has efficient systems in place that can be used to disburse new types of cash transfers. The government credits the payouts to bank accounts that most Singaporeans have already registered with the government. Those who do not have a registered bank account will receive a cheque that is mailed to their registered residential address. If the cheque is not encashed or banked in within six months, the government will credit the payouts into the individuals' defined contribution accounts, which are withdrawable within a year. The set-up for determining eligibility and disbursing payouts suggests that Singaporeans who are eligible for the SSS payouts will almost certainly receive their payouts.

Data Source
Our data comes from the Singapore Life Panel (SLP), a new longitudinal monthly survey, which aims to follow a population-representative sample of about 15,000 Singapore citizens and permanent residents aged 50 -70 and their spouses. The survey is conducted by the Centre for Research on the Economics of Aging (CREA), and it captures a rich set of data including demographic characteristics, labour decisions, private cash transfers, and expenditure. More details on the SLP can be found in Vaithianathan et al. (2017).
We use data from waves 0 -23 of the SLP, covering the period May 2015 to Jun 2017. This data allows us to implement a difference-in-differences (DiD) identification strategy, since SSS details were announced in end-Mar 2016 and payouts were disbursed from end-Jul 2016 onwards.
Before we move on, we highlight two advantages of using this dataset, compared to surveys which collect data at lower (i.e. yearly or longer) frequencies. First, the high frequency at which the SSS is collected enables us to precisely time, and separately estimate the announcement and disbursement effects of the SSS. Capturing the announcement effect allows us to avoid underestimating the SSS's effects (Blundell et al., 2011). Second, the SLP also allows us to directly test the validity of the DiD identifying assumption of parallel trends, which other studies that use data from surveys with only two or three time points cannot do.

Sample and Variables
Our main analysis focuses on the impact of receiving Silver Support Scheme (SSS) payouts.
Thus, we restrict our sample to those who would be age-eligible to receive SSS payouts from 2016 onwards (i.e. those aged 65 and above in 2016). In addition, our sample includes only Singapore citizens who live in public housing flats 13 (two of the eligibility criteria for SSS receipt). This reduces the extent of heterogeneity within our sample. The Singapore Life Panel also contains a rich set of demographic variables which we use to compare individuals who received SSS against those who did not, and refine our identification strategy by restricting our sample to individuals who are demographically more similar (more details on our identification strategy in Section 4).

Summary Statistics
In Table 1, we show summary statistics that compare baseline demographics between those who received SSS and those who did not. Focusing on the left panel, we see that the proportion of respondents who received the Silver Support Scheme (SSS) payouts (as determined by our key treatment variable described in Section 3.2) is approximately 26%. This is within the range anticipated by the policymakers. Across the range of demographic variables, the differences in means between those who received SSS and those who did not are mostly statistically significant and in the expected direction. For example, recipients are less likely to live in 5-room flats, and they feel less financially prepared for retirement.
While differences in characteristics between treatment and control groups do not necessarily invalidate our chosen identification strategy (i.e. difference-in-differences (DiD)), there could be concerns that these differences are sufficient to lead to non-parallel trends in our outcome variables in the absence of treatment, which would then violate the DiD identifying assumption. As alluded to at the end of Section 3.2, we will address this concern by restricting our sample using the method we will describe in Section 4.

Identification Strategy
We implement a difference-in-differences (DiD) strategy to estimate the causal average treatment-on-treated effect of receiving Silver Support Scheme (SSS) payouts on labour decisions, private cash transfers, and expenditure. Our sample consists of Singapore citizen respondents aged 65 and above in 2016 who live in public housing flats. The treated group comprises those who received SSS payouts, and the control group those who did not. As discussed in Section 3.2, our treatment variable takes value one if individuals reported that they received at least one payout in 2016. This means that treatment status is exogenous, as eligibility for SSS payouts in 2016 was pre-determined before the announcement of SSS details. Such a treatment definition may attenuate our treatment effects, as some members of the control group may be treated; we address this by performing a robustness check where we restrict the control group to those who definitely did not receive SSS payouts (see Section 5).
To tackle the possibility that our treatment and control groups may be sufficiently different to violate the DiD identifying assumption of parallel trends in the absence of treatment, we restrict our sample to individuals who are more similar demographically. We do so by first estimating the propensity score of being a SSS recipient using the data-driven algorithm described in Imbens (2015) on a rich set of baseline demographic characteristics. The propensity score is eventually estimated based on the following selection of covariates and some of their interactions: age as at 2016, marital status, gender, ethnicity, education, public housing flat-type, whether respondent's father is still living, number of household members, number of living children, income of self and spouse, self-assessment of financial preparedness for retirement and satisfaction with one's economic situation. We then exclude individuals with either very low or high propensity scores, and retain a sample which includes only those with propensity scores from 0.2 to 0.8.
Trimming the sample in this way improves the comparability of the treatment and control groups (see right panel, Table 1). Most differences in mean values of demographic characteristics are no longer statistically significant, and the magnitude of the normalised differences are small (the largest is 0.14). (The normalised differences are computed as the difference in means standardised by the square root of the mean variance of both groups (Imbens, 2015)). The distributions of variables related to the SSS eligibility criteria for both the control and treatment groups also became more similar (Figure 1). The improved similarity of both groups increases the probability that the DiD identifying assumption will be met.
Having said this, we acknowledge that the improved similarity of both groups in terms of observables does not necessarily imply improved similarity in unobservables. However, remaining differences in unobservables are unlikely to lead to differences in trend between the treated and control groups as our treatment definition excludes the possibility of self-selection into receiving SSS payouts.
In addition, we check the validity of the DiD identifying assumption for our study more directly. We do so by performing visual checks (by plotting the unconditional means of our outcome variables), and statistical checks (by including placebo leads in our empirical specificationsee Section 4.2). Our checks suggest that our identifying assumptions are generally valid. We discuss the results of these checks in more detail in Section 6.

Main Specifications
Our key regression specification is used to estimate the overall effects of Silver Support Scheme (SSS): and are our main coefficients of interest, capturing the treatment effects during the announcement and disbursement periods respectively. ,the coefficients for our placebo leadsare used to test the validity of the difference-in-differences (DiD) identifying assumption in our study. A statistically insignificant , would give us more confidence that the assumption is valid.
As individuals' behaviour may take time to adjust, we also estimate equation (2) to study the dynamics of the effect over time: where , is a dummy variable that takes value 1 if month belongs to quarter . We split the post-disbursement period into quarters, such that includes dummies for the periods August-September 2016, Oct-December 2016, January-March 2017, and April-May 2017 16 .
Lastly, we carry out a series of heterogeneity analyses, to examine if the SSS's effects vary by net assets, subjective financial preparedness for retirement, flat-type (a proxy for wealth and the determinant of payout quantum), and gender. We do so by interacting the treatment variables × and × with the variables listed above. The variables for the heterogeneity analyses were chosen as the effects of permanent income shocks on the outcomes we study are likely to vary by wealth / liquidity constraints, amount received, and gender (see, e.g., Jappelli & Pistaferri, 2010;Kaushal, 2014;Hernani-Limarino & Mena, 2015).

Potential Threats to Identification and Robustness Checks
While we have attempted to construct sufficiently similar treatment and control groups that are likely to satisfy the DiD identifying assumptions, some identification issues may remain. Here, we describe a series of robustness checks designed to address these potential issues. These checks include the use of different control / treatment groups and different re-weighting techniques to address potential failures of the parallel trends assumption and mismeasurement issues, as well as the use of different specifications of equation (1) to test the sensitivity of our main estimates. The results of these checks are summarized in Section 6; full results are in Appendices A -C.
First, there may be measurement error with respect to our treatment variable. A significant proportion of individuals defined as treated reported that they received at least one payout for 2016, but not for 2017. This is likely to be driven by misreporting, as the nature of the eligibility 16 The last quarter ends in May instead of June 2017 because the Jun 2017 wave of the SLP captures outcome values that correspond to behaviours in May 2017 (e.g. respondents were asked whether they received income from work in the previous month).
criteria make it unlikely for SSS receipt status to change dramatically in the short run. In addition, some control individuals may have received SSS payouts, as they reported that they received SSS payouts in 2017 but not 2016. Both types of measurement error may attenuate the estimated effects of receiving SSS payouts.
To study whether attenuation from the sources above is an issue, we estimate the following regression: where , is a dummy variable that takes value 1 if the individual belongs to subset . Our coefficients of interest are those related to subset (i)the subset least likely to suffer from misreporting. These coefficients are based on the comparison between those who almost certainly received SSS payouts (i.e. subset (i)) and those who almost certainly did not receive SSS payouts (i.e. suppressed subset), thus reducing potential attenuation from the sources of mismeasurement described above. If these estimates are similar to those from our main regression, attenuation is less likely to be a major issue in our study.
Second, even though respondents in our control group do not receive SSS payouts, their outcomes may still be affected by the SSS if his/her spouse receives SSS payouts 18 . This may attenuate our main estimates.
To account for this, we re-define our treatment groups so that they are based on the number and identity of SSS recipients within a household, and estimate the following equation 19 : where is a dummy variable that takes value 1 if either respondent i or respondent i's spouse received SSS; ℎ _ , can be a dummy variable indicating that (i) only the respondent received SSS; (ii) only the respondent's spouse received SSS; or (iii) both the respondent and his/her spouse received SSS. The control group in this regression is thus made up of respondents who did not receive SSS payouts, and whose spouse did not receive SSS payouts either.
To give us a sense of whether attenuation is a major problem for our main estimates, we compare our main estimates to the coefficients related to the subset in which only the respondent received SSS payouts. Other coefficients in this specification allows us to explore whether effects vary when the number of people in a household receiving SSS increases.
Third, to address concerns that our main specification's control group is not ideal, we reestimate equation (1) using an alternative control group selected from younger individuals who are not age-eligible for SSS payouts yet (i.e. those aged 56 to 63 20 in 2016) 21 . We estimate the propensity of receiving SSS payouts for these younger individuals (using the coefficient estimates from our earlier logistic regression described in Section 4.1), and define the alternative control group as those with propensity scores of 0.2 -0.8, to match the propensity scores for our treatment group in our main regression. In addition to using younger respondents as an alternative control group, we also apply different re-weighting techniques on our original control group to address differences in baseline covariates between the control and treatment groups. (More details at the end of the next paragraph.) Fourth, using the original control group, we test the sensitivity of our results by estimating different variations of equation (1) where we: (i) remove placebo leads to check if our results are sensitive to our choice of the baseline period; (ii) restrict the sample to individuals with at least one observation in each of the pre-announcement, announcement-to-disbursement and postdisbursement periods, to check that compositional differences are not driving our results; (iii) add group-specific time fixed effects (based on ethnicity and flat-types) to allow for differential time trends in different groups; (iv) add age fixed effects; (v) add control covariates on other welfare 20 We excluded individuals aged 64 in 2016 as some of them would be receiving SSS payouts for the year 2017. 21 Using age-ineligible controls may lead to attenuation of our results if individuals who are age-ineligible but expect to receive SSS payouts in future start adjusting their behaviour even before they are age-eligible. This is unlikely to be an issue in our caseour results in Section 7 suggest that such anticipatory behaviour does not exist in our sample. payments 22 ; (vi) implement Abadie (2005)'s semiparametric DiD 23 and DiD matching using 1-to-1 nearest neighbour matching to check if our results are robust to different re-weighting methods used to address imbalances in baseline characteristics.

Results
In this section, we discuss the effects of receiving SSS on each type of outcome variablelabour decisions, private cash transfers, and expenditure.

Labour decisions
Receiving SSS payouts appears to have had little, if any, effect on the labour-related outcomes we study in this section. Table 3 reports the overall effect of receiving SSS payouts on labour-related outcomes (specified at top of each column). The coefficients for the placebo leads are statistically insignificant. This observation, together with the similar pre-treatment trends we observe in Figure 2, suggest that the parallel trends assumption is likely to hold for this set of variables. The coefficients for the announcement and disbursement effects of SSS, and , are statistically insignificant across all variables studied. These coefficients are also close to zero for column (1) (which looks at whether an individual received income from work in the last month), and positive for columns (2) and (3) (which look at the amount of income received from work) 24 . Our point estimate for the probability of engaging in paid work is lower than the fall of 4 to 6 percentage points that many other studies on non-contributory pensions find (Aguila et al.,22 These controls are not included in our main specification as these questions are posed at lower frequency and therefore, not all respondents reply to these questions. This leads to a considerable decrease in our sample size. 23 This method addresses the imbalance of baseline characteristics between the treated and control groups by reweighting control observations based on their propensity score; control observations with a higher propensity score are given a higher weight. We use the Stata package absdid described in Houngbedji (2015) to implement this estimator. 24 Column (2) includes individuals who did not work; the income for these individuals are taken to be zero. The results for column (2) thus capture effects from both the extensive and intensive margin. Column (3) (4)). However, recipients' expectations readjusted very quickly -SSS recipients' self-assessed probability of working full-time at 70 rose quickly soon after, and was no longer statistically significant in 2017. In addition, we find little evidence that these effects vary substantially by recipients' net assets, subjective financial preparedness for retirement, flat-type, or gender. (Results available on request.) These results are robust to the series of robustness checks we described in Section 5 (see Appendix A for results). In particular, attenuation of our results due to mismeasurement / having a spouse receive SSS payouts does not seem to be an important issue for this set of outcomes, as the treatment effects estimated from regressions where we try to address attenuation (equations (3) and (4)) are similar to, or smaller than treatment effects we estimate using our main specification (equation (1)).
In all, we find no evidence that receiving SSS reduced labour supply along either the extensive or intensive margins in the first year of the SSS's implementationour estimates are statistically insignificant and either negative and close to zero, or positive. In addition, receiving SSS does not appear to have a persistent impact on future work expectations. However, there is suggestive evidence that SSS recipients' behaviour may not have fully adjusted yet, and that their labour supply may fall further in future.

Private cash transfers
Receiving SSS payouts appears to have had little impact on whether recipients gave or received private cash transfers. A concern for this set of results is that our identifying assumption may not hold as well for variables related to whether SSS recipients received private cash transfers.
While the placebo leads in Table 5 are statistically insignificant, Figure 3 shows that there seems to be a spike in the variables related to transfers received by SSS recipients, at approximately one or two months before the SSS announcement. Nonetheless, as we will see later in this sub-section, our robustness checks give us similar results, giving us more confidence that receiving SSS payouts has had little effect on private transfers.  (1) and (4) respectively), and positive for variables related to the amount of private transfers received (columns (2) and (3) suggest that it is unlikely that private transfers to SSS recipients fell along the intensive margin.
There does not appear to be a clear pattern in how transfers received and given by SSS recipients change over time (Table 6), and the effect does not appear to vary substantially by recipients' net assets, subjective financial preparedness for retirement, flat-type, or gender (results available on request).
Lastly, our results are robust to the series of checks we describe in Section 5 (see Appendix B for results). In particular, robustness checks that partially address our concern of potentially different time trends between the treated and control groups in our main specification produce similar results (see Table B3 and columns (7) and (8) of Tables B4 -B7 where an alternative control group and other re-weighting schemes are considered 27 ). The estimated coefficients of the placebo leads from these checks are generally similar, or smaller in magnitude than those from our main estimates, suggesting that the parallel trends assumption may hold better in these specifications. Among the robustness checks where the parallel trends assumption appears to hold better, the estimated announcement and disbursement effects are generally similar to, or smaller in magnitude than estimates from our main regression. In addition to the robustness checks we describe in Section 5, we study the SSS's effects on transfers using a separate set of questions on annual transfers (results available on request). As these questions are asked annually, they may be subject to less of the month-to-month variability we observe for our main set of transfer-related variables. Our results in this sub-section are robust to estimations from this separate set of annual questions. Finally, our robustness checks designed to deal with potential attenuation of the estimated SSS effects also show that attenuation is unlikely to be a serious issue in this case ( Table   B1 and Table B2).
In all, our results suggest that in the first year of the SSS's implementation, receipt of SSS payouts was unlikely to have crowded out private cash transfers from friends and family to SSS recipients, and was unlikely to have led to a rise in recipients giving cash transfers to others.

Expenditure
Our ability to make definitive statements about the effect of the SSS on expenditure is hampered by the imprecision of our estimates. We therefore relegate our detailed discussion of our expenditure-related results to Appendix C in the interest of space. Briefly, our ability to make definitive statements about the effect of SSS on total and non-durables expenditure is hampered by the imprecision of our estimatesour point estimates are positive and quite large in magnitude, but statistically insignificant. In addition, our identifying assumption does not seem to hold well for durables expenditure, even though the effects are positive and statistically significant.
Therefore, these expenditure-related results need to be interpreted with caution, and corroborated by studies using other datasets before a more definitive conclusion can be made.

Supplementary analyses on anticipation effects
Finally, we carry out supplementary analyses to explore whether younger individuals, who are not age eligible to receive SSS payouts yet, change their behaviour when they expect to receive SSS payouts in the future. Our sample for this analysis is restricted to those who are aged 56 -63 in 2016, and therefore age-ineligible for the SSS over the period we study. Our estimation strategy in this section follows the strategy we laid out for our main results in Section 4, though the treated group is now defined as those who expect to receive SSS payouts in future 28 .
We do not find any evidence that expecting to receive the SSS led to changes in labourrelated decisions, private cash transfers or expenditure (see Appendix D)our estimated announcement and disbursement effects are all statistically insignificant and close to zero (especially for labour-related decisions and private cash transfers). This result is not too surprising, as individuals who expect to receive SSS payouts in future are likely to be liquidity / credit constrained, and are unlikely to be able to adjust their behaviour before they receive payouts (see e.g. Jappelli & Pistaferri, 2010;Galiani et al., 2016).

Conclusion
This paper adds to the literature on the effects of non-contributory pensions on labour decisions and private cash transfers, by using a difference-in-differences strategy and a new highfrequency panel dataset to evaluate the effect of a new non-contributory pension from Singapore (the Silver Support Scheme, or SSS). We find no evidence that SSS recipients reduced their labour supply, experienced persistent changes in the subjective probability that they will be working fulltime past age 70, received fewer cash transfers from or gave more cash transfers to family and friends. Our results are robust to the battery of robustness checks described in Section 5, that include the use of different control groups, different reweighting methods, and the addition of group-specific time fixed effects. However, we do find weak evidence that the adjustment in recipients' labour supply may not be complete yet. Lastly, we do not find any evidence of anticipatory effectsindividuals who are not yet age-eligible for the SSS but expect to receive the SSS in future do not exhibit changes in labour supply, work expectations, private transfers, or expenditure.
We emphasise that these are results for the first year of the SSS's implementation, and individuals' behaviour may not have fully adjusted yet. It would therefore be useful to revisit this question in the future, to study the SSS's effects in the medium and long run. In addition, it would be useful to evaluate the effect of the SSS using larger datasets (e.g. administrative datasets), to improve the precision of the estimated effects. Nonetheless, we highlight that the magnitude of the In all, our results, when coupled with the finding in a companion paper that the SSS improved recipients' subjective well-being (Chen & Tan, 2017) 29 , suggest that the SSS was successful in improving recipients' welfare without substantial reductions in labour supply, crowding out of private transfers, or changes in the behaviour of younger individuals who expect to receive SSS payouts in future. In addition, our results from this paper suggest that the effects of noncontributory pensions are likely to vary by institutional and socio-economic context as well as payout levels. It will thus remain important to evaluate introductions of, or reforms to noncontributory pensions, to obtain more generalizable evidence on the effects of non-contributory pensions.  (2015) (as the difference in means standardised by the square root of the mean variance of both groups) 3 ***, **, * represent statistical significance at the 10%, 5% and 1% levels respectively, based on a t-test.   (1) (2). The sample is restricted to respondents who are age-eligible for SSS (i.e. aged 65 and above in 2016), Singapore citizens, live in public housing flats, and with a propensity score of 0.2 -0.8.  (3) and (6) include only responses with positive values. 3 Results are estimates of coefficients in eq (1). The sample is restricted to respondents who are age-eligible for SSS (i.e. aged 65 and above in 2016), Singapore citizens, live in public housing flats, and with a propensity score of 0.2 -0.8. 4 Mean and standard deviation statistics are based on pre-announcement levels of the dependent variable for respondents who received SSS payouts.  (3) and (6) (1) (1) (1) (8) show results from additional robustness checks carried out. These checks are: (1) removal of the lead terms; (2) restricting the sample to a "balanced" panel, where each individual has at least one observation in the preannouncement, announcement-to-disbursement, and post-disbursement periods; (3) allowing for ethnicity-specific time fixed effects; (4) allowing for flat-type-specific time fixed effects; (5) adding age fixed effects as a control; (6) adding receipt of additional welfare payments (Workfare Income Supplement; GST Vouchers) as a control-sample is smaller because this data is not collected every wave and not everyone responds every wave; (7) reweighting each observation by their propensity of receiving SSS as in Abadie (2005); and (8) DiD matching with a 1-1 nearest neighbour match. Eq (1) describes the baseline model used in these checks. 4 For columns (1) -(6), the sample is restricted to respondents who are age-eligible for SSS (i.e. aged 65 and above in 2016), Singapore citizens, live in public housing flats, and with a propensity score of 0.2 -0.8. The number of observations in these columns refers to the number of individual-month observations. For columns (7) and (8), the number of observations refers to number of respondents, and the sample is not restricted by the propensity score. The sample, however, is smaller than the full sample due to data availability issues specific to the estimation of (7) and (8).  (8) show results from additional robustness checks carried out. These checks are: (1) removal of the lead terms; (2) restricting the sample to a "balanced" panel, where each individual has at least one observation in the preannouncement, announcement-to-disbursement, and post-disbursement periods; (3) allowing for ethnicity-specific time fixed effects; (4) allowing for flat-type-specific time fixed effects; (5) adding age fixed effects as a control; (6) adding receipt of additional welfare payments (Workfare Income Supplement; GST Vouchers) as a control-sample is smaller because this data is not collected every wave and not everyone responds every wave; (7) reweighting each observation by their propensity of receiving SSS as in Abadie (2005); and (8) DiD matching with a 1-1 nearest neighbour match. Eq (1) describes the baseline model used in these checks. 4 For columns (1) -(6), the sample is restricted to respondents who are age-eligible for SSS (i.e. aged 65 and above in 2016), Singapore citizens, live in public housing flats, and with a propensity score of 0.2 -0.8. The number of observations in these columns refers to the number of individual-month observations. For columns (7) and (8), the number of observations refers to number of respondents, and the sample is not restricted by the propensity score. The sample, however, is smaller than the full sample due to data availability issues specific to the estimation of (7) and (8).   (8) show results from additional robustness checks carried out. These checks are: (1) removal of the lead terms; (2) restricting the sample to a "balanced" panel, where each individual has at least one observation in the preannouncement, announcement-to-disbursement, and post-disbursement periods; (3) allowing for ethnicity-specific time fixed effects; (4) allowing for flat-type-specific time fixed effects; (5) adding age fixed effects as a control; (6) adding receipt of additional welfare payments (Workfare Income Supplement; GST Vouchers) as a control-sample is smaller because this data is not collected every wave and not everyone responds every wave; (7) reweighting each observation by their propensity of receiving SSS as in Abadie (2005); and (8) DiD matching with a 1-1 nearest neighbour match. Eq (1) describes the baseline model used in these checks. 4 For columns (1) -(6), the sample is restricted to respondents who are age-eligible for SSS (i.e. aged 65 and above in 2016), Singapore citizens, live in public housing flats, and with a propensity score of 0.2 -0.8. The number of observations in these columns refers to the number of individual-month observations. For columns (7) and (8), the number of observations refers to number of respondents, and the sample is not restricted by the propensity score. The sample, however, is smaller than the full sample due to data availability issues specific to the estimation of (7) and (8).  (3) and (6) (3) and (6) include only responses with positive values. 3 Results are estimates of coefficients in eq (4). In the interest of space, we do not show the coefficients from the placebo leads. The sample is restricted to respondents who are age-eligible for SSS (i.e. aged 65 and above in 2016), Singapore citizens, live in public housing flats, and with a propensity score of 0.2 -0.8.   (8) show results from additional robustness checks carried out. These checks are: (1) removal of the lead terms;

Appendix B: Robustness checks for private cash transfers
(2) restricting the sample to a "balanced" panel, where each individual has at least one observation in the preannouncement, announcement-to-disbursement, and post-disbursement periods; (3) allowing for ethnicity-specific time fixed effects; (4) allowing for flat-type-specific time fixed effects; (5) adding age fixed effects as a control; (6) adding receipt of additional welfare payments (Workfare Income Supplement; GST Vouchers) as a control-sample is smaller because this data is not collected every wave and not everyone responds every wave; (7) reweighting each observation by their propensity of receiving SSS as in Abadie (2005); and (8) DiD matching with a 1-1 nearest neighbour match. Eq (1) describes the baseline model used in these checks. 4 For columns (1) -(6), the sample is restricted to respondents who are age-eligible for SSS (i.e. aged 65 and above in 2016), Singapore citizens, live in public housing flats, and with a propensity score of 0.2 -0.8. The number of observations in these columns refers to the number of individual-month observations. For columns (7) and (8), the number of observations refers to number of respondents, and the sample is not restricted by the propensity score. The sample, however, is smaller than the full sample due to data availability issues specific to the estimation of (7) and (8). 1 Standard errors clustered at the household level in parentheses. ***, ** and * represent statistical significance at the 1%, 5% and 10% level of significance respectively. 2 All transfer values are reported at the couple (respondent and spouse if respondent is married) and monthly level. 3 Columns (1) - (8) show results from additional robustness checks carried out. These checks are: (1) removal of the lead terms; (2) restricting the sample to a "balanced" panel, where each individual has at least one observation in the preannouncement, announcement-to-disbursement, and post-disbursement periods; (3) allowing for ethnicity-specific time fixed effects; (4) allowing for flat-type-specific time fixed effects; (5) adding age fixed effects as a control; (6) adding receipt of additional welfare payments (Workfare Income Supplement; GST Vouchers) as a control-sample is smaller because this data is not collected every wave and not everyone responds every wave; (7) reweighting each observation by their propensity of receiving SSS as in Abadie (2005); and (8) DiD matching with a 1-1 nearest neighbour match. Eq (1) describes the baseline model used in these checks. 4 For columns (1) -(6), the sample is restricted to respondents who are age-eligible for SSS (i.e. aged 65 and above in 2016), Singapore citizens, live in public housing flats, and with a propensity score of 0.2 -0.8. The number of observations in these columns refers to the number of individual-month observations. For columns (7) and (8), the number of observations refers to number of respondents, and the sample is not restricted by the propensity score. The sample, however, is smaller than the full sample due to data availability issues specific to the estimation of (7) and (8). 1 Standard errors clustered at the household level in parentheses. ***, ** and * represent statistical significance at the 1%, 5% and 10% level of significance respectively. 2 All transfer values are reported at the couple (respondent and spouse if respondent is married) and monthly level. 3 Columns (1) - (8) show results from additional robustness checks carried out. These checks are: (1) removal of the lead terms; (2) restricting the sample to a "balanced" panel, where each individual has at least one observation in the preannouncement, announcement-to-disbursement, and post-disbursement periods; (3) allowing for ethnicity-specific time fixed effects; (4) allowing for flat-type-specific time fixed effects; (5) adding age fixed effects as a control; (6) adding receipt of additional welfare payments (Workfare Income Supplement; GST Vouchers) as a control-sample is smaller because this data is not collected every wave and not everyone responds every wave; (7) reweighting each observation by their propensity of receiving SSS as in Abadie (2005); and (8) DiD matching with a 1-1 nearest neighbour match. Eq (1) describes the baseline model used in these checks. 4 For columns (1) -(6), the sample is restricted to respondents who are age-eligible for SSS (i.e. aged 65 and above in 2016), Singapore citizens, live in public housing flats, and with a propensity score of 0.2 -0.8. The number of observations in these columns refers to the number of individual-month observations. For columns (7) and (8), the number of observations refers to number of respondents, and the sample is not restricted by the propensity score. The sample, however, is smaller than the full sample due to data availability issues specific to the estimation of (7) and (8).

Appendix C: Expenditure-related results
In general, we are unable to make definitive statements about this set of outcomes, due to the imprecision of our estimates. There is some evidence of a rise in durables expenditure, but our identifying assumption does not seem to hold well for durables expenditure. These results thus need to be interpreted with caution. The rest of this section discusses our results on the effect of receiving the SSS on expenditure-related outcomes in more detail. Table C1 reports the effect of receiving SSS payouts on recipients' expenditure (at the couple level 34 ). The coefficients related to the announcement and disbursement effects are generally quite large in magnitude, but imprecise and thus statistically insignificant across the variables studied. However, there is some evidence of a rise in durables-related expenditure during the announcement-to-payment and post-disbursement periods, as well as a small rise in expenditure related to clothes and personal care in the announcement-to-payment period. Table C2 shows that there is little evidence that the consumption response to receiving SSS payouts has changed over time, though the increased expenditure on durables may be concentrated in the announcement-to-payment and early disbursement period. In general, the effect does not seem to vary substantially by recipients' flat-type or gender, though there is suggestive evidence that SSS recipients who are more financially prepared for retirement / have higher income may spend more on health-related consumption (results available on request).
A concern with these results, however, is that the identifying assumption may not hold up well for some variables. Our identification assumption appears to hold reasonably well for total and non-durable expenditurethe placebo leads in Table C1 are statistically insignificant, and the trends plotted in Figure C1 suggest that the pre-treatment trends for the treated and control 34 Respondent and spouse if the respondent is married.
groups are similar. However, while the placebo leads for expenditure on durables are statistically insignificant, the pre-treatment trends for the treated and control groups look quite different. Figure   C1 suggests that our durables-related results could be driven by the trend difference in the pretreatment period: the pre-treatment trend for the control group falls much more quickly than that of treated group at the start; this could lead to an over-estimation of the effect of SSS on durables expenditure among the treated 35 . Unfortunately, the robustness checks that could potentially address the issue of differing time trends between the treated and control groups do not appear to be very effective, as the coefficients of the placebo leads are often large and sometimes marginally significant (see Table C5 and columns (7) and (8) of Table C6 - Table C9 36 ). Our durablesrelated estimates in all specifications in this paper may thus be overestimated 37 .
Apart from the potential issue of differing time trends between the control and treatment groups, the other robustness checks designed to address potential attenuation (Table C3 and Table   C4) and test the sensitivity of our results to other specification (Table C5 -Table C9) show that our results seem to be robust to these issues. Our results are also robust to transforming our variables using the inverse hyperbolic sine, which approximates the natural logarithm but maps zero to zero (see e.g. Burbidge et al., 1988;MacKinnon & Magee, 1990) (results available on request).
In all, we find little evidence that the SSS led to increases in total and non-durables expenditure, and some suggestive evidence that durables expenditure may have risen in response to SSS receipt. Unfortunately, our ability to make definitive statements about the lack of an effect 35 To a lesser extent, this may be a potential issue for total and non-durable expenditure as well. This issue biases our results upwards, and means that SSS receipt is even less likely to have had much of an effect on these total and nondurable expenditure. 36 To recap, we use age-ineligible controls (Table C5) and different reweighting methods (Abadie (2005)'s semiparametric DiD and 1:1 matching DiD in columns (7) and (8) of Table C6 -Table C9) to address potential issues with the parallel trends assumption in our main estimates. 37 To a lesser extent, total and non-durables expenditure face this issue as well.
of the SSS on total and non-durables expenditure is hampered by the imprecision of our estimates.
In addition, our identifying assumption does not seem to hold well for durables expenditure; these results thus need to be interpreted with caution. Our expenditure-related results should thus be corroborated by studies using other datasets before a more definitive conclusion can be made.
A -17 Non-durables are based on the difference between total expenditure and durables. The sub-categories of non-durables captured in columns (5) -(9) are not exhaustive. 3 Results are estimates of coefficients in eq (1). The sample is restricted to respondents who are age-eligible for SSS (i.e. aged 65 and above in 2016), Singapore citizens, live in public housing flats, and with a propensity score of 0.2 -0.8. 4 Mean and standard deviation statistics are based on pre-announcement levels of the dependent variable for respondents who received SSS payouts. Non-durables are based on the difference between total expenditure and durables. The sub-categories of non-durables captured in columns (5) -(9) are not exhaustive. 3 Results are estimates of coefficients in eq (2). The sample is restricted to respondents who are age-eligible for SSS (i.e. aged 65 and above in 2016), Singapore citizens, live in public housing flats, and with a propensity score of 0.2 -0.8.  (5)   Notes: 1 Standard errors clustered at the household level in parentheses. ***, ** and * represent statistical significance at the 1%, 5% and 10% level of significance respectively. 2 Dependent variables are shown at the top of each column. All expenditure values are reported at the couple (respondent and spouse if respondent is married) and monthly level. Total expenditure excludes cash gifts. Durables include furniture/furnishings, household appliances, home and vehicle repair/maintenance. Durables subset includes only furniture/furnishings and household appliances. Non-durables are based on the difference between total expenditure and durables. The sub-categories of non-durables captured in columns (5) -(9) are not exhaustive. 3 Results are estimates of coefficients in eq (4). In the interest of space, we do not show the coefficients from the placebo leads. The sample is restricted to respondents who are age-eligible for SSS (i.e. aged 65 and above in 2016), Singapore citizens, live in public housing flats, and with a propensity score of 0.2 -0.8.   (8) show results from additional robustness checks carried out. These checks are: (1) removal of the lead terms; (2) restricting the sample to a "balanced" panel, where each individual has at least one observation in the preannouncement, announcement-to-disbursement, and post-disbursement periods; (3) allowing for ethnicity-specific time fixed effects; (4) allowing for flat-type-specific time fixed effects; (5) adding age fixed effects as a control; (6) adding receipt of additional welfare payments (Workfare Income Supplement; GST Vouchers) as a control-sample is smaller because this data is not collected every wave and not everyone responds every wave; (7) reweighting each observation by their propensity of receiving SSS as in Abadie (2005); and (8) DiD matching with a 1-1 nearest neighbour match. Eq (1) describes the baseline model used in these checks. 4 For columns (1) -(6), the sample is restricted to respondents who are age-eligible for SSS (i.e. aged 65 and above in 2016), Singapore citizens, live in public housing flats, and with a propensity score of 0.2 -0.8. The number of observations in these columns refers to the number of individual-month observations. For columns (7) and (8), the number of observations refers to number of respondents, and the sample is not restricted by the propensity score. The sample, however, is smaller than the full sample due to data availability issues specific to the estimation of (7) and (8).      (2015) (as the difference in means standardised by the square root of the mean variance of both groups) 3 ***, **, * represent statistical significance at the 10%, 5% and 1% levels respectively 4 This is a self-assessment on preparedness for retirement, captured on a scale of 1 to 5, with a higher value representing greater preparedness. This was captured during the baseline survey, which was conducted before the announcement of details on the Silver Support Scheme. Notes: 1 N refers to the number of observations at the respondent-wave level 2 These variables are reported at the couple level (respondent and spouse if respondent is married). 3 These variables include observations with zero values, e.g. if respondent did not receive any income from work, amount of income will be recorded as 0. Notes: 1 Standard errors clustered at the household level in parentheses. ***, ** and * represent statistical significance at the 1%, 5% and 10% level of significance respectively.  (1). The sample is restricted to respondents who are not age-eligible for SSS (i.e. aged 56 to 63 in 2016), Singapore citizens, live in public housing flats, and with a propensity score of 0.2 -0.8. 4 Mean and standard deviation statistics are based on pre-announcement levels of the dependent variable for respondents who expected to receive SSS payouts. Notes: 1 Standard errors clustered at the household level in parentheses. ***, ** and * represent statistical significance at the 1%, 5% and 10% level of significance respectively. 2 Dependent variables are shown at the top of each column. All transfer values are reported at the couple (respondent and spouse if respondent is married) and monthly level. Columns (3) and (6) include only responses with positive values. 3 Results are estimates of coefficients in eq (1). The sample is restricted to respondents who are not age-eligible for SSS (i.e. aged 56 to 63 in 2016), Singapore citizens, live in public housing flats, and with a propensity score of 0.2 -0.8. 4 Mean and standard deviation statistics are based on pre-announcement levels of the dependent variable for respondents who expected to receive SSS payouts.
A -31 Notes: 1 Standard errors clustered at the household level in parentheses. ***, ** and * represent statistical significance at the 1%, 5% and 10% level of significance respectively. 2 Dependent variables are shown at the top of each column. All expenditure values are reported at the couple (respondent and spouse if respondent is married) and monthly level. Total expenditure excludes cash gifts. Durables include furniture/furnishings, household appliances, home and vehicle repair/maintenance. Durables subset includes only furniture/furnishings and household appliances. Nondurables are based on the difference between total expenditure and durables. The sub-categories of non-durables captured in columns (5) -(9) are not exhaustive.