Since it is not possible to test our identification assumption directly, we examine several potential threats to the assumption indirectly and check to what extent the estimated coefficients of the hidden curriculum confound other mechanisms, if at all.
Do parental choices result in biased estimates?
As already discussed in Sect. 3.3, parents’ school choice is a typical endogeneity issue. Here, we further test the possible influence of parents’ school choice using different datasets. First, we examine the achievement gap between schools in Japan using the data from the Third International Mathematics and Science Study (TIMSS 1995). If the academic curriculum is heterogeneous across the country and/or if self-sorting into schools is common, the achievement gap should be more prominent between schools than within schools. The results in Table A2, in Online Appendix II, show that between-school disparities in test scores are considerably small in Japan compared with those in the United States and England. Surprisingly enough, in Japan, between-school disparities are smaller than within-school disparities.Footnote 13 This supports the discussion in Sect. 3.3 that the national academic achievement test was not publicly disclosed before the 2000s.
Second, we explore the link between school districts and land values. If parents recognize quality schools and value those with good academic performance, land values may be affected by school district boundaries. In several developed countries, school districts affect property values (Black and Machin 2010). Thus, we investigate the effect of school zone boundaries on land prices using land value data in the Tokyo metropolitan area, where people are reputed to be more education-minded (see Online Appendix III). The results show that land values are significantly different from town to town in the Tokyo metropolitan area, but the difference in school zones in a town does not influence land values.Footnote 14
These results indicate that endogenous sorting into elementary schools (and thus, sorting by educational content/practices) is very unlikely in Japan. The remaining concern may be that people are more interested in the non-academic curriculum than the academic one. However, it is more difficult to observe the hidden curriculum (and its consequences) than the academic one, and therefore it is not realistic or rational that school choices are made based on the hidden curriculum. Logical reasoning also implies that such endogeneity is unlikely. If egalitarian education cultivates a cooperative attitude in people, parents with such attitudes are more likely to send their children to schools providing egalitarian education, or advocate changing the curriculum in an egalitarian direction. However, assuming that our results are driven by endogenous school choice, this would mean that parents must be aware of the specific influences of the hidden curriculum beforehand: in particular, the positive effects of participatory/cooperative education on pro-social preferences and the negative effects of anti-competitive education. However, it is not reasonable to presume that people know that participatory/cooperative and anti-competitive education, both of which are referred to as egalitarian education, have opposite influences.
Finally, we conduct a robustness check on the estimates to explore possible parental influence. If parents consider the curriculum in their child’s school to be unfavorable, they may attempt to change it through the parents’ association, or move to another school zone in which a preferred education is provided. We cannot directly observe these events from our dataset, but if they are more likely to happen after observing the schooling of a first-born child, we can detect this possibility by restricting the sample to first-borns. That is, the content/practices for any children born after the first child are considered to be endogenously determined. Panel A of Table 9 reports the results for the basic specification (as in Table 7) using the sub-sample of first-born children, a sample size of 2,005.Footnote 15 Although it is expected that excluding the sub-sample of second- or later-born children attenuates the estimates in size, our estimates remain mostly unchanged or increase in their magnitude.
Table 9 Robustness checks on coefficients of hidden curriculum. Do other confounding factors result in biased estimates?
We further examine the possibilities that unobserved factors other than parental choices confound the impact of the hidden curriculum on social preferences. First, we eliminate the possible influence of the revisions of the School Curriculum Guidelines.Footnote 16 As discussed in Sect. 3.2, the identifying variations in the hidden curriculum stem from the generational and prefectural differences in actual educational content and practices. Although prefecture fixed effects are controlled in Table 7, there still exists the possibility that our results are driven by unobserved generational differences within prefectures. A candidate for the source of such heterogeneity might be the appearance of differing versions of the guidelines over time, and therefore we additionally control dummies for the guideline versions and their interactions with prefecture dummies (at the age of 12). Estimation results are presented in Panel B of Table 9, showing that coefficient estimates remain virtually unchanged in magnitude. Thus, unobserved heterogeneity within prefectures due to the revision of the guidelines is unlikely to influence our estimates.
Second, we address the possible influence of unobserved heterogeneity within prefectures by controlling dummies for administrative units smaller than prefectures. Because geographical or cultural factors within prefecture, or community characteristics, may confound our estimates of the hidden curriculum’s influence, we check the possible influences indirectly by controlling city/ward/county (shi/ku/gun) fixed effects. The estimation results in Panel C show that, after controlling city/ward/county dummies, coefficient estimates are either almost unchanged or increase in magnitude, and contrasts still exist between “anti-competition” and “participation & cooperation.” Therefore, unobserved heterogeneity within prefectures is less likely to influence our results.
Finally, we feel it necessary to mention the possibility of omitted variable bias due to unobserved teacher characteristics. One might doubt that unobserved teacher characteristics affect the selection of educational content/practices and that our estimates capture the influence of such teachers’ personal qualities rather than the hidden curriculum. Fundamentally, we do not rule out the possibility of such influences through teachers because the hidden curriculum is considered to be partly based on the preferences, beliefs, and norms of teachers.
At the same time, however, we believe that, in our context, it is unlikely that our estimates confound the influence of unobserved teacher characteristics for the following reasons. First, pupils do not have the same teacher for the entirety of their primary education and therefore, the effect of a particularly influential teacher would be “smoothed out” by teachers with different levels of influence in other years. In addition, an influential teacher would not have the same level of influence on all pupils in a class or year (i.e., what some people find engaging, others might not). Moreover, our educational content/practices used in the analysis (as listed in Table 1) cannot be determined at the class (teacher) level but at the school level. Furthermore, given that, as a general rule, teachers cannot choose the schools in which they work, educational content/practices at schools are expected to be independent of teachers’ personal characteristics. In fact, Table A1 in Online Appendix I suggests that our proxies for the hidden curriculum vary widely by prefecture: within-prefecture variations are much smaller than between-prefecture variations. This is mainly due to the educational administration system in Japan, implying that actual educational content/practices are determined at some community level.
Our estimations in Tables 7 and 8 include several controls that capture the quality of a teacher or a school (school district), such as class size, dummies for experience with classroom chaos, teachers’ active intervention with bullying, and the number of high schools that can be chosen in a school district. In addition, current individual income level, which might partially capture the quality of education, is also controlled. Therefore, our estimates are unlikely to suffer from unobserved teacher characteristics.
Does the way the hidden curriculum is measured matter?
Another potential threat to the parameter identification is that the hidden curriculum used in this study is based on respondents’ retrospective and subjective answers on past educational content/practices. A typical issue regarding retrospective data is recall bias. For instance, more intense experiences might remain in respondents’ memory. Moreover, when people hold two conflicting cognitions, they might distort one to mitigate the dissonance of the other (issue of cognitive dissonance). In other words, there is a possibility that current preferences distort reports of past experiences.
In fact, as we saw in Table 2, a non-negligible number of respondents answered “do not remember.” If such forgetfulness occurs in a non-random manner due to recall bias, it is possible that our proxies for the hidden curriculum are correlated with unobserved individual preferences or beliefs. However, this may not be a serious problem. The content/practices with high rates of “do not remember” answers are those with large regional differences. For example, “school assembly on atomic bomb day” is practiced mainly in western Japan. This is because Hiroshima and Nagasaki are in western Japan, and the school assembly is held during summer vacation to ensure the terrible lessons of the war are not forgotten. Therefore, memories of the school assembly are strongly connected with the date for those who experienced it. Likewise, “emergency drill on September 1” is associated with the Great Kanto Earthquake, which struck on September 1, 1923, and is, therefore, predominantly practiced in eastern Japan including the Kanto region. Thus, answering “do not remember” to a content/practice reflects the fact that the respondent received education that placed less emphasis on such content/practice. Due to this, one would expect many respondents to answer “do not remember” where they otherwise might have answered “no.” As such it seems a justified approach would be to treat the answers “do not remember” and “no” as the same.
To check the influence of recall bias empirically, we also estimate several specifications, additionally controlling for the percentage of “do not remember” answers to the 17 educational content/practices or 17 dummy variables that take unity if the answer is “do not remember,” and zero otherwise. Panel D reports the coefficient estimates of the hidden curriculum variables employing the dummy variables’ specification. Although the statistical significance of some estimates decreases, the magnitude is almost unchanged. Thus, controlling for these variables does not affect our main findings. In addition, we conduct further checks for the possibility of recall bias. Table A3 in Online Appendix IV reports the estimation results where the dependent variables are “do not remember” dummies and the explanatory variables are eight social preferences and other controls. If answering “do not remember” is attributable to recall bias, we may observe that people with some kind of social preference are more or less likely to answer “do not remember” to a specific educational content/practice. The estimation results, however, mostly show no evidence of the linkage between current preferences and “do not remember” answers. Even for the exceptions that show statistically-significant relationships, no convincing evidence exists pointing to recall bias as an explanation of our findings in Table 7. Thus, it is unlikely that people intentionally forgot the educational content/practices they received or that people strongly affected by an educational content/practice are more likely to remember that content/practice.
Finally, we check the sensitivity of our results to the measurement of the hidden curriculum. Panel E shows the results using group-averages of dummy variables on the 17 educational content/practices. We divide the 17 educational content/practice dummies into several groups according to their correlation coefficients and calculate the average by group (see Online Appendix V). Because the standard deviation of factor scores used in Table 7 is unity, the group-averages are also standardized so that their standard deviation becomes unity for ease of comparison. As can be seen from the results in Panel E, the magnitude of coefficient estimates is remarkably stable. In addition, employing polychoric factor analysis with the principle factor (PF) method, instead of the PCF method used in Table 7, does not affect the results (see Online Appendix V). Therefore, our findings are not sensitive to the measurement of “hidden curriculum” variables.
Other issues
Finally, we examine two issues associated with the outcome and treatment variables used in the analysis. The first issue is about the specification of the dependent variables. As mentioned in Sect. 3.2, we converted respondents’ five-scale answers regarding social preferences into binary responses and estimated the linear probability model of Eq. (1). To check the robustness of our results and the sensitivity to this choice, we implemented the probit model with the binary responses and the ordered probit model with the original five-scale responses. Estimation results, which are reported in Table A7 in Online Appendix VI, show that the OLS estimates in Table 7 are considerably similar to the probit and ordered probit estimates. In the case of the probit estimation, rather, the coefficient estimates are slightly larger in their magnitudes than the OLS estimates in most cases. Thus, our main findings are not sensitive to the choice of the dependent variables and method.
The second issue is a so-called generated regressor problem. The proxies for the hidden curriculum we employ are generated from the factor analysis. Hence, potential differences between the proxies and the actual hidden curriculum may render our estimation invalid. When the measurement errors are correlated with the proxies, an OLS regression causes bias in our estimates. In this case, however, if the classical measurement error assumptions hold, the attenuation bias exists and our estimates can be considered as the lower bound of the impacts. On the other hand, when the proxies for the hidden curriculum are independent of the errors, there is no problem in estimating the impacts, but caution is needed in estimating the standard errors, since the measurement errors are included in the unobserved components of the outcome, \( \varepsilon_{i} \) in Eq. (1). Therefore, we check this issue by applying the Jackknife method.Footnote 17 The Jackknife cluster robust standard errors are reported in Panel F of Table 9. The panel shows that the standard error increases slightly and the statistical significance decreases in some cases, but the changes are not so large as to compromise our main findings.