Imagine if this is a Singaporean official what will happen

《ブッダの言葉》 自分の都合に執着してはいけません 執着を捨てる喜びを知りなさい ブッダは「～であるべき」「～してほしい」という自分中心の都合（執着）こそが、イライラや不安、怒りを生み出す原因であると見抜いていました。状況や他人は、自分の都合に合わせては動いてくれないからです。

自分自身が思うがままにならないのに 他人が思うがままになるはずがない

May you also be on the path of liberation from your dopamine addiction! PS - get an e ink phone today, hurry hurry! 🤎

Trump just keeps chasing and chasing. But has he reached his goal? Has he realized he can never truly be satisfied?

A Singapore university study reports lower grades during hotter semesters, despite widespread air-conditioning. It also finds that access to cooled dorm rooms helps. The accessible material does not settle whether heat does most of its damage during studying, sleep or exams. Analysis by Astra. This was a limited audit of accessible public material and headline arithmetic. The full manuscript download was blocked, so the detailed methods and tables remain unverified. 1. The reported loss is roughly one mark. Hongyan Li, Haoming Liu, Alberto Salvo and Rhita Simorangkir studied undergraduate course records from 2005–2019 at one leading Singapore university. They report that moving from the coolest to the hottest semester in their seasonally adjusted sample reduces performance by 1.5%. The paper's public results preview puts average marks at 69.4 out of 100. A 1.5% reduction is about 1.04 marks. Astra's arithmetic check using the rounded heat coefficient and raw exposure range also gives approximately a one-mark loss at the larger reported coefficient. That supports the headline's approximate size. It does not reproduce the exact season-adjusted comparison or verify its confidence interval. The available material did not supply enough information to check uncertainty independently. 2. Access to cooling leaves several questions open. An air-conditioner can be available without being used throughout the day or night. Students also spend time outside their rooms. For students living at home, the public introduction describes a measure based on expected air-conditioning penetration in their residential building. That is less direct than measuring cooling in each student's home. A remaining association with heat therefore does not demonstrate that cooling technology has reached its limit. Nor does a benefit from cooled bedrooms establish better sleep as the explanation. Cooling can also change where and how students study. Separating these explanations requires assessment dates, clearly separated exposure periods and, for a sleep mechanism, direct sleep evidence. The inaccessible full paper may contain additional timing checks. 3. The dorm comparison has a useful strength and an unresolved condition. The authors compare students who applied for oversubscribed air-conditioned dorms. Restricting the comparison to people who wanted cooling reduces an obvious difference in preferences. But excess demand is not itself random assignment. The crucial evidence is how rooms were allocated, whether applicants remained comparable after refusals or moves, and whether other heat-relevant dorm features differed. For example, ventilation or study spaces could affect the response to hot weather alongside bedroom cooling. These are conditions to verify, not demonstrated flaws in the study. The allocation documentation and direct statistical comparison of heat effects would determine how strongly to interpret the cooling result. 4. The population limits remain important. This is evidence about selected university students. It does not supply a numerical effect for primary-school children. The authors also did not find robust evidence that lower-income students were more heat-sensitive. That does not prove equal vulnerability, but it does rule out presenting this study as having demonstrated a class divide. The defensible conclusion is that the reported results challenge the idea that widespread cooling access automatically removes heat-related academic losses. The next useful check is the full manuscript and appendix, especially the dorm allocation rule, timing analysis and uncertainty estimates. Paper: doi.org/10.1016/j.jebo.2025.…

《ブッダの教え》 モノが無くても苦しむが、有ったら有ったで同じように苦しむ。 田畑や家、お金や地位が無ければ、それらを求めて苦しみ、有れば、管理や維持のためにまた苦しむ。そのほかのものにしても、皆同じである。『仏説無量寿経』 これをお釈迦様は「有無同然」といわれました

Bolded means need to check the Claim lol

Used Jev to build a Dharma Lens chrome extension.

Jev is like BERT, but you dont need to train it, and it's much much smarter

A Singapore study links infant care with stronger achievement and some behavioural difficulties. It does not establish that childcare itself causes that tradeoff. Analysis by Astra. The underlying research is by Kristy Jia Jin Lee and Wei-Jun Jean Yeung, published in Child Development in June 2026. The study followed 2,580 children in 2,187 households across two survey waves. It compared children whose non-parental care began by 18 months with children who had parental care during infancy. The latter group could use childcare later. 1. The achievement findings deserve attention. Trained interviewers assessed reading and mathematics directly. Both centre-based and home-based infant care were associated with higher initial achievement, measured when children were at least three. Most achievement results remained statistically significant after Astra adjusted for the study's 16 main direct comparisons together. For example, centre care was associated with an initial mathematics score 5.8 W-score points higher than parental infancy care, with a 95% confidence interval from 2.8 to 9.0. W scores measure achievement on the test's scale; these are not IQ points. The estimate also describes an adjusted association, not a proven benefit from changing care. The behavioural pattern was less straightforward. Centre care predicted more parent-reported difficulties initially. But both care types predicted smaller later increases in externalizing difficulties, such as defiance and hyperactivity, in the direct model paths. That does not prove that earlier differences disappeared. It does make “infant care increases behavioural problems” an incomplete summary. 2. Family pressures remain a possible explanation. The authors already make substantial adjustments. They use propensity weights to make observed family characteristics more comparable, account for survey selection and attrition, and report checks involving children from the same household. Those methods cannot adjust for an important history that was not measured. Employment several years after infancy does not tell us a parent's work schedule or stress before childcare began. Earlier family pressures could affect both care choices and later child outcomes. 3. The proposed parenting sequence was not observed. Parenting stress, punitive parenting and initial child behaviour were measured in the same survey wave. This cannot establish that care increased stress, which then increased punishment, which then changed behaviour. Child difficulties could also increase parental stress and discipline. The authors acknowledge this limitation. Astra checked the complete supplementary results: none of the 12 indirect parenting paths to subsequent behavioural change had a confidence interval excluding zero. That leaves the mechanism unresolved; it does not prove it is absent. 4. The reporter comparison needs the same outcome. Achievement was independently assessed, while parents reported behaviour and parenting. Stress might affect those reports, but it might also accompany real difficulties. Comparing achievement with behaviour changes both the outcome and the reporter. A more informative check would compare parent and teacher or observer ratings of the same behaviour. Astra also found eight mismatches between baseline p-values in the main and sensitivity tables, plus an unresolved scale for weekly care hours. These need the authors' code to reconcile. They do not establish that the main results are wrong. This was an audit of public documents and published numbers. The original child data and analytical code require a request to the authors, so their models were not rerun. The paper alone does not justify changing a family's childcare arrangements. It supports further investigation of care and the pressures surrounding parents, without establishing which intervention would help. The next useful steps are to reproduce the models and obtain stress, parenting and behavioural measurements in a clear time sequence. academic.oup.com/chidev/adva…

Pastpipatkul and Ko’s 2025 paper studies happiness and income across 78 countries from 2006 to 2023. It reports small, mixed income effects and stronger positive roles for generosity and freedom, interpreting the findings through Buddhist ideas. Analysis by Astra finds that the paper does not establish causal effects or test the Buddhist mechanisms it invokes. Its numerical associations remain unverified because published tables contain contradictions and the original analysis could not be rerun. 1. The question is useful, but the conclusions exceed the evidence. The study asks how income and social conditions relate to national average life evaluations. Its reported 1,404 country-year observations repeatedly measure 78 countries. They do not track individual Buddhist practitioners. The authors report uncertainty, discuss mixed signs and acknowledge cultural differences. These are useful qualifications. Astra’s checks also confirm that the sample counts match the stated 18-year period. That arithmetic cannot establish whether the underlying data were assembled correctly. 2. Some published values are impossible under the stated definitions. Astra found that high-income social support, a proportion bounded between zero and one, has a reported mean of 1.1804 and maximum of 80.5. A crisis indicator described as zero or one has a reported maximum of 13.232 in low-income countries. Several crisis statistics exactly repeat unemployment statistics from the preceding row. A copying error is plausible. These contradictions establish reporting problems, but they do not reveal whether the fitted model used incorrect data. They are not evidence of fabrication. 3. The uncertainty prevents confident claims about direction or importance. Astra checked all 17 published predictor intervals for coefficients described as constant over time. Sixteen have their endpoints in the correct order, and every one of those 90% intervals includes zero. The remaining interval has its endpoints reversed. This does not prove that the effects are absent. It means the intervals allow both positive and negative values, so the sign of the central estimate alone cannot support a confident directional claim. Comparing coefficient sizes also cannot establish that generosity matters more than income. The predictors use different units. The paper additionally reports coefficients that change over time, but the missing fitted specification prevents Astra from establishing how those components combine. The sampling diagnostics give further reason for caution. A reported diagnostic called R-hat reaches 1.15 for low-income freedom, raising concerns about the reliability of the simulation used to estimate the model. The paper treats sampling diagnostics as evidence of model fit, although these answer different questions. 4. The measured variables do not establish the Buddhist explanation. “Freedom” measures satisfaction with life choices. “Generosity” uses a charity-donation response adjusted for income. Neither directly measures freedom from craving, the motive for giving or non-attachment. National life evaluation does not directly measure liberation from suffering. Those distinctions leave room for philosophical interpretation. They prevent this analysis from demonstrating that the proposed Buddhist mental processes explain the results. No Buddhist practice or such mental process was measured. The causal claims have a separate gap. Astra found no paper-specific argument establishing that changing a predictor would change happiness, rather than both reflecting other conditions. Bayesian estimation does not supply that argument by itself. Paper: [Buddhist Thought on Happiness and Income Growth Relations Across Varying Income Countries](link.springer.com/article/10…)

A sweetener review reporting 3.6 million participants used a diabetes estimate from before the original study adjusted for dieting and body weight. Kim and colleagues' May 2026 meta-analysis reported associations with diabetes, hypertension, heart failure, stroke and mortality. The supplied headline numbers match the paper. The harder question is what those numbers can establish. 1. One input represents a different adjustment level. The diabetes forest plot uses de Koning's hazard ratio of 1.91, adjusted only for age. That study followed 40,389 men and recorded 2,680 diabetes cases over 20 years. After fuller adjustment, including health status, dieting, weight change and body mass index, its estimate was 1.09, with a 95% confidence interval of 0.98–1.21. Yet the meta-analysis lists those broader adjustments alongside the study while plotting the age-only result. [Original study](pmc.ncbi.nlm.nih.gov/article…) The audit reconstructed the pooled diabetes estimate from the 16 printed rows: HR 1.26, interval 1.14–1.40. Replacing only that input produced about 1.20, interval 1.11–1.30. This is a sensitivity check, not a corrected meta-analysis. Other inputs still need checking, and several rows reuse participants from the same cohorts. Separate estimates of caffeinated and caffeine-free drinks do not create independent groups of people. Neither do estimates of consumption frequency and duration from the same women. 2. The two reviews ask different questions. The cautious January 2026 review explicitly excluded studies focused on artificially sweetened beverages. It found 11 articles, split between dietary consumption and blood measurements, and described the dietary evidence as limited and mixed. That is a different evidence set from the larger review. Its conclusion is not proof that the same association was tested and disproved. The audit could verify its abstract, but not obtain its full paper. [January review](doi.org/10.1093/nutrit/nuaf2…) 3. Replacing sugar differs from replacing water. A randomized-trial review found that replacing sugary drinks with low/no-calorie alternatives reduced body weight by about 1.06 kg, with a 95% interval of 0.41–1.71 kg lower weight. The relevant direct comparisons involved 601 adults. Median follow-up across the review's trials was 12 weeks. This supports a modest weight benefit, not a claim about lifelong cardiovascular safety. [Trial review](pmc.ncbi.nlm.nih.gov/article…) Water comparisons are less uniform. In SODAS, 181 adults with established diabetes who habitually drank diet drinks were randomized to continue them or replace them with water. Over 24 weeks, HbA1c, a measure of blood-sugar control, changed less favourably in the water group by 0.29 percentage points (standard error 0.12). That result concerns existing users with diabetes. It does not establish that healthy water drinkers should start consuming sweeteners. [SODAS](pmc.ncbi.nlm.nih.gov/article…) 4. Confounding does not explain away every concern. NutriNet-Santé reported cardiovascular associations that persisted after several attempts to address health-related switching. Modeled substitution studies also remain observational, even when their comparisons better match a real dietary decision. [NutriNet-Santé](bmj.com/content/378/bmj-2022…) Erythritol and xylitol experiments provide evidence about clotting mechanisms. But blood levels can reflect the body's own production, and small, acute experiments do not establish long-term clinical harm. Findings about these sugar alcohols cannot automatically be assigned to aspartame or sucralose. [Erythritol](pmc.ncbi.nlm.nih.gov/article…), [xylitol](pmc.ncbi.nlm.nih.gov/article…) The six scores for Kim's review are: - Design fit: 3/5. Observational synthesis suits an association question, but the pooled studies use different designs and comparisons. - Measurement quality: 2/5. Verified adjustment and study-description errors weaken confidence in the extracted inputs. - Analysis and robustness: 2/5. Repeated cohort contributions and a consequential adjustment mismatch limit trust in the pooled estimates. - Transparency and reproducibility: 3/5. Printed estimates permit a diabetes-pool reconstruction, but the authors' analysis inputs were unavailable for checking. - Claim discipline: 4/5. The authors acknowledge confounding, contrasting trial findings and the inability to establish causality. - Generalizability: 3/5. The broad evidence base combines populations and sweetener measurements that limit product-specific conclusions. Rebuilding the inputs by cohort, adjustment level, sweetener and comparator could change this rating if the revised estimates remain stable. A reliable answer must specify what is being replaced, in whom, and which outcome is measured. Paper: doi.org/10.4162/nrp.2026.20.…

Singapore's Ministry of Finance reported falling income inequality and most children earning more than their fathers in its February 2026 report on inequality and social mobility. Analysis by Astra: the income decline holds up within the published measures. The evidence does not establish falling wealth inequality or improving chances of moving up the income ranking. 1. The income decline survives separating the measures. From 2015 to 2025, the employment-income Gini after taxes and transfers fell from 0.409 to 0.359 among resident households with someone employed. The Gini measures inequality; lower means less unequal. The broader market-income measure, covering all resident households, fell from 0.437 to 0.379 after taxes and transfers. Both figures use household income per member. These are separate series, not an old employment figure joined to a new market figure. The 2025 estimates are preliminary. 2. Broader income coverage brings comparability limits. Market income adds sources such as interest, rent and pensions. Including households without anyone employed also brings retirees and other non-employed households into the distribution. But SingStat's [technical note](singstat.gov.sg/files/ec1bd2…) says royalty data start in 2018 and private transfers received in 2021. The available components therefore differ across the decade. The public tables cannot show how much that changes the trend. CPF contributions, CPF interest and valued government benefits also mean these income measures do not describe only cash available for everyday spending. 3. Earning more than a father is different from climbing the ranking. Among eligible children born in 1985–1989 whose fathers were in the bottom income fifth, 96% earned more than their fathers after inflation. Only 13.8% reached the top fifth of their own generation's income distribution. Both results can hold because incomes can rise without people's relative positions changing. These comparisons use employment incomes averaged over five years, with fathers representing parental income. Mothers' incomes are not included in that parental measure. Relative ranks are measured at ages 30–38 for children and about 46 on average for fathers. All three mobility charts apply a no-income exclusion. The wording does not establish whether one income-free year is enough to exclude someone or whether income must be absent throughout the measurement window. Without the selection rules and excluded-family counts, these results cannot describe all families. The direction of any selection bias is also unresolved. The bottom-to-top share fell from 14.5% for children born in 1978–1982 to 13.8% for those born in 1985–1989. MOF acknowledges this moderation. Its three reported birth groups include overlapping cohorts. No sample sizes or uncertainty estimates are provided to establish statistical significance. 4. Wealth mobility remains unanswered. The report's first official household wealth-Gini estimate, for 2023, is a snapshot. It cannot show whether wealth inequality is falling. International wealth comparisons also depend on which pension rights, housing and other assets count. In an [April 2026 parliamentary reply](mof.gov.sg/news-resources/ne…), MOF said the longitudinal, intergenerational wealth data needed to study wealth mobility were not yet available. Children earning more than their fathers does not answer how assets and inherited advantage pass between generations. 5. One small error is demonstrable. The report says home equity exceeds half of average wealth in every wealth quintile. Its own table gives about 45.9% for the fourth quintile, matching two charts showing 46%. Rounding cannot explain the difference. That sentence needs correction, but the income-inequality finding does not depend on it. Astra checked public sources, definitions and arithmetic, not original household records. The supported conclusion is declining measured income inequality. Extending it to broader equality requires more evidence. The next useful checks are the exact mobility selection rules and an income series with the same components throughout. Source: [MOF, Income Growth, Inequality, and Social Mobility Trends in Singapore, 9 February 2026](isomer-user-content.by.gov.s…)

Chua and Zhang's “Housing Markets and the Belief in Opportunity” reports that housing-price and tax messages can reduce optimism about children's prospects in Singapore. It raises a useful question: whether expensive housing changes people's beliefs about who can get ahead. Analysis by Astra. The evidence supports a cautious claim about immediate survey responses. It does not yet establish that bad news has a larger psychological effect than comparable good news. 1. The main result holds up as reported arithmetic. The researchers recruited 3,160 adults in October-November 2025 and analysed 2,299 after exclusions. Participants received one of four housing messages or no information, then described where hypothetical children from families near the bottom or top of society would end up as adults. For children starting in the bottom fifth, rising-price information lowered expected adult position by 0.101 rung on a five-rung scale. The tax message lowered it by 0.104 rung. Approximate 95% uncertainty intervals run from declines of 0.197 to 0.005 rung and 0.200 to 0.008 rung, respectively. The paper's “about 12%” comparison checks out. It means 12% of the initial perceived gap between children from bottom- and top-status families. It does not mean a 12% reduction in children's actual chances of advancing. The authors also report similar effects after relaxing some exclusions. That strengthens the case that the main pattern is not entirely explained by those filters. 2. The comparison between bad and good news is still unresolved. The favourable-message estimates are small and uncertain. That alone does not establish that their effects differ from the adverse-message effects. The comparisons share a control group, so their uncertainty must be calculated jointly. Astra checked how the answer changes under different assumptions about that dependence. The published tables do not provide enough information to settle the comparison. A difference between signed responses also needs to be distinguished from a test of equal negative and positive responses. Neither adverse effect survives Astra's correction across the four bottom-origin tests. This is a sensitivity check, not proof that nothing happened. 3. The messages differ in ways that could explain the pattern. The rising-price message shows accumulated price increases. The favourable price message shows prices increasing more slowly. Slower growth leaves the earlier increase largely intact. Participants did lower their price forecasts after that message, so it was not simply ignored. There is also a concrete tax-information problem. The displayed increase from S$8,730 to S$11,980 is correct for the 2023-to-2024 schedules at an annual rental value of S$100,000. But by the late-2025 survey, the corresponding amount was S$8,620 before rebates under the [updated IRAS schedule](iras.gov.sg/quick-links/tax-…). The screen also broadly describes rates rising for most homes. [IRAS's 2024 annex](iras.gov.sg/docs/default-sou…) says rates were unchanged for about 90% of owner-occupied properties, including all HDB flats. Tax bills could still change through property valuations. A response to this screen does not establish the response to a complete account of the policy. 4. The outcome is narrower than lasting pessimism about one's own children. The main measure concerns hypothetical children, and responses were collected within the same survey. There is no later follow-up establishing persistence. The manuscript describes broader adult recruitment than a homeowners-only sample, but does not provide the final tenure counts needed to assess renters or prospective first-time buyers separately. Housing information may influence beliefs about opportunity. The next useful check is a direct comparison using the joint uncertainty and full randomized-sample results. Establishing psychological asymmetry would then require better-matched messages and follow-up measurements. [Paper: Housing Markets and the Belief in Opportunity](abfer.org/media/abfer-events…)

Statin eligibility may now cover 87.5 million Americans. How much benefit should someone expect before committing to years of treatment? An AI audit of the new US guideline, the JAMA eligibility analysis and STAREE checked the published claims and absolute-risk arithmetic. The evidence supports cardiovascular prevention. A favorable lifetime trade-off for every newly eligible low-risk adult remains unestablished. AI editorial ratings: STAREE's stated trial claims receive a provisional 4/5. The JAMA eligibility estimate remains not rated pending its full methods. 1. Eligibility covers different decisions. Anderson, Wilson and Sussman's JAMA analysis estimated that 56.6% of nonpregnant US adults aged 30–79 without known atherosclerotic cardiovascular disease, which includes heart attacks and strokes, qualify under the guideline. The 95% confidence interval was 54.2–58.9%. That population includes people already taking statins. The guideline also separates treatment that is recommended from treatment that is reasonable to consider after discussion. The 87.5 million figure cannot be read as 87.5 million new prescriptions with equally strong supporting evidence. [JAMA analysis](doi.org/10.1001/jama.2026.11…). 2. STAREE strengthens the evidence for healthy older adults. Zoungas and colleagues randomized 9,971 Australians aged at least 70, without cardiovascular disease, diabetes or dementia, to atorvastatin 40 mg daily or placebo. Over a median 5.9 years, the cardiovascular outcome occurred in 297 treated participants versus 412 on placebo. The hazard ratio was 0.70, indicating about a 30% lower rate of first events, with a 95% confidence interval of 0.61–0.82. The raw proportions differ by about 23 events per 1,000 participants, although unequal follow-up means that is not an exact six-year treatment estimate. The outcome includes cardiovascular death, heart attack, stroke and procedures to restore blood flow in coronary arteries. Investigators added the procedure component after a blinded review found fewer events than expected. That change was documented, but the headline cannot be described as a 30% reduction in heart attacks and strokes alone. The trial did not demonstrate longer survival free of dementia or persistent disability. Its estimate, HR 0.94 with a 95% interval of 0.84–1.05, still allows meaningful benefit as well as no benefit. Statistical uncertainty is not proof that treatment has no effect. 3. Starting risk changes the absolute benefit. Consider an explicitly hypothetical person with a valid untreated ten-year cardiovascular risk of 3%. Assume treatment reduces that same risk by 25% throughout the decade. Risk falls from 3% to 2.25%. That is 7.5 events prevented per 1,000 people treated for ten years, or roughly 133 treated per event prevented. It is not a STAREE result or an individual forecast. The guideline's own illustration assumes larger relative reductions: 35% for moderate-intensity treatment and 45% for high intensity. Applied at 3% starting risk, those assumptions imply roughly 95 or 74 treated per event prevented over ten years. The answer depends on achieved cholesterol reduction and whether the assumed effect applies to the person and outcome. [Guideline, Figure 4](news.randox.com/wp-content/u…). 4. A lifetime judgment needs benefits, harms and preferences. Randomized evidence identifies increased diabetes diagnoses, a small excess of muscle symptoms and more abnormal liver tests. Their severity and persistence differ greatly from a disabling stroke. Simply subtracting one category's event count from another gives no reliable measure of overall health gained. Long-term estimates also need credible untreated risk, aging, deaths from other causes, adherence and the burden someone attaches to daily medication. Extrapolating a six-year trial into twenty years cannot resolve those assumptions. The evidence supports discussing statins with eligible people using absolute benefits and recommendation strength. The next useful check is STAREE's full appendix: the original cardiovascular outcome, individual components, risks at common follow-up times and detailed harms. Those tables were unavailable to this audit, so a complete trial-specific benefit/harm calculation remains unfinished. These ratings are editorial judgments on each study's own claims, not a validated scale or probabilities of correctness. STAREE: Overall 4/5, provisional. Its decisive strength is the randomized cardiovascular result; the main audit limitation is unavailable detailed results. Component, safety or missing-data findings could change this rating. - Design fit: 4/5. Randomization against placebo directly addresses treatment effects. - Measurement quality: Not assessed. Detailed event adjudication and missingness were unavailable. - Analysis and robustness: Not assessed. Final models and sensitivity results remain unchecked. - Transparency and reproducibility: Not assessed. Protocol and analysis-plan passages were accessible, but full results and data access were not verified. - Claim discipline: 4/5. The abstract distinguishes cardiovascular benefit from unproven disability-free benefit. - Generalizability: 4/5. The result supports the studied healthy older population; broader patient groups remain unverified. JAMA eligibility analysis: Overall not rated. A national survey fits the prevalence question, but the unavailable eligibility code and survey methods prevent a firm judgment. Checking those materials would permit a rating. - Design fit: 4/5. A national survey is appropriate for estimating eligibility. - Measurement quality: Not assessed. Exact eligibility coding and exclusions remain unchecked. - Analysis and robustness: Not assessed. Weighting, uncertainty calculations and sensitivity checks were unavailable. - Transparency and reproducibility: Not assessed. Full methods and code access were not established. - Claim discipline: 4/5. The abstract estimates eligibility without demonstrating lifetime treatment benefit. - Generalizability: Not assessed. Representativeness after exclusions and weighting requires the full methods. [STAREE: original NEJM paper](doi.org/10.1056/NEJMoa260731…).

Honestly, when building actual production workflows, I dont just evaluate intelligence scores, but also hallucination scores. Intelligence is already sufficient in terms of what we need it for, so I think the Chinese labs should actually also focus on reducing hallucination if they want us to use it more wide-spread in production.

A Singapore study links fathers’ paternity leave to some better outcomes for children. Using Singapore Longitudinal Early Development Study data, the paper links fathers’ leave-taking to paternal involvement, family relationships and aspects of children’s development. It uses structural equation modelling and propensity-score matching as a sensitivity analysis. The results are not uniformly positive across every developmental outcome and pathway. The verdict: interesting associations, with causality still unresolved. The study gives reasons to investigate the benefits of leave. It does not establish that taking leave caused the improvements, or that prior family differences explain them away. What held up ✅ The researchers compared fathers reported to have taken one week or at least two weeks of leave with those reported to have taken none. Surveys in 2018–2019 and 2021 followed children aged 3–8 across the two waves. The authors adjusted for many obvious differences: education, employment, income, household arrangements and mothers’ gender attitudes. Their sensitivity analysis also used propensity methods to make groups more comparable on measured characteristics. Children completed interviewer-administered tests of letter-word identification and applied problems. That matters: the achievement results do not depend solely on a parent saying their child is doing well. The achievement analyses included 1,774 children; behavioral analyses included 1,780. These were repeated observations, with some children sharing households, in two-parent families where mothers were initially the primary caregivers. But three issues limit what the results can tell us. 1. The fathers may have differed before leave. Imagine a father already committed to caregiving. He might be more likely to take leave and remain involved years later. A supportive employer could also make both easier. Matching families on income or education cannot remove differences that were never measured. These examples are possible explanations, not biases the audit has demonstrated or quantified. Many controls were measured years after leave. They are not necessarily a record of what the families were like beforehand. The paper acknowledges missing information on fathers’ prenatal involvement and attitudes. Its own limitations section says causality cannot be established conclusively. 2. The proposed family mechanisms are harder to establish. The paper examines whether leave is linked to children’s development through fathers’ involvement and family relationships. But mothers retrospectively reported leave-taking and also reported several family measures. Behavior was caregiver-reported, and the first-wave family measures and child outcomes were collected together. A parent’s perceptions could influence several answers. Children’s difficulties could also affect family relationships. Following children into a second survey helps. It does not settle which direction the first-wave relationships run. 3. The results depend on which outcome—and which statistical test—you examine. The models split associations into direct parts and indirect parts through family processes, then add them for a total. These statistical labels do not establish causes. For fathers taking at least two weeks, the later behavioral association was not statistically significant overall, although a modeled indirect component was. A significant component does not make the total significant; an uncertain total does not prove no benefit. Astra checked the reported results using Holm correction, which limits false positives when assessing multiple tests together. Each group covered two leave comparisons, three outcomes and two waves: - Direct associations: none of 12 tests survived. - Combined indirect associations: one of 12 survived—the first-wave behavioral result for at least two weeks of leave. - Total associations: zero to two of 12 could survive. Exact p-values were unavailable to settle the count. Those test groupings were chosen retrospectively for this audit. They were not the authors’ prespecified rule or the only defensible grouping. The evidence did not all disappear. What this leaves us with Leave-taking predicted some better outcomes after measured adjustment. How much reflects leave itself remains unresolved. Astra inspected accessible sources and checked published-summary arithmetic. This was not an original-data replication; the supplement and original-data checks remain incomplete. Analysis by Astra 🔎, auditing Nanxun Li and Wei-Jun Jean Yeung’s [2025 paper](doi.org/10.1111/jomf.13100) in the Journal of Marriage and Family.