A synthetic-control estimate of Washington’s school finance reform
The Seattle Times has opened a series, Educating Washington, on the perennial questions of the state’s schools. Its first installment asks: Is WA meeting its constitutional commitment to education? (Bazzaz 2026). The commitment in question is the opening sentence of the constitution’s education article:
It is the paramount duty of the state to make ample provision for the education of all children residing within its borders without distinction or preference on account of race, color, caste, or sex.
Dahlia Bazzaz’s answer runs mostly through inputs. Since the Supreme Court’s 2012 decision in McCleary v. Washington, and the $100,000-a-day contempt fine that followed, K–12 has become the largest item in the state budget. It bought smaller classes, some of the highest teacher pay in the country, and per-student spending just above the national average. On that reading, yes: the state has met its commitment, or at least the court said so when it released the Legislature from its supervision in 2018.
The series promised a second installment on “what results the state gets, and doesn’t get, for its substantial investment,” and that is the better question. The framers did not write “paramount duty” in order to get a budget line. They wrote it to get educated children. Whether the state is meeting its commitment is a question about results, and the constitution’s spirit is the standard that the money is supposed to serve, not the other way around.
The installment has now run (Superville 2026). Denisa Superville reports that state, local, and federal education revenue rose from $13.4 billion in 2012–13 to more than $21 billion in 2024–25, in today’s dollars, while NAEP reading and math scores “inched up then largely flatlined.” The people she interviews then argue past each other. Marguerite Roza of Georgetown’s Edunomics Lab says “we are not seeing any parallel progress in math and reading given the size of the investments.” Superintendent Reykdal says the results would have been worse without the money. Senate Majority Leader Jamie Pedersen says there are “too many variables that changed for you to conclude that our funding was inadequate or a mistake,” and calls the investments “sound.”
All three are claims about a counterfactual — what Washington’s scores would have been without McCleary — and none of them is tested against one. The article does reach for other states: Washington ranks 18th in per-pupil spending (17th among states; the ranking counts the District of Columbia), 27th of 38 states in math recovery since the pandemic (Dewey et al. 2026), and Mississippi, which spends less, has raised its reading scores. But a ranking is a snapshot, not a comparison with what Washington itself would have done, and neither it nor the trend lines shown below can distinguish Roza’s reading from Reykdal’s and Pedersen’s. This document supplies the missing comparison, and a benchmark for how large the effect should have been.
Here is what the results look like, put next to the money, before any statistical machinery is applied:
naep_all <- build_naep_panel()
wa_pt <- dplyr::filter(panel, state == TREAT_UNIT)
lead_np <- naep_all |>
dplyr::filter(jurisdiction %in% c(TREAT_UNIT, "NP")) |>
dplyr::select(jurisdiction, year, score) |>
tidyr::pivot_wider(names_from = jurisdiction, values_from = score) |>
dplyr::mutate(lead = .data[[TREAT_UNIT]] - NP)
plot_money_vs_results(panel, naep_all)
Real, cost-adjusted revenue per student rose 31% between the last test before the ruling and 2019. Washington’s grade 8 math score, on the one test that is the same in every state, ended that period 2.3 points lower than it began it, and its lead over the national average slipped from 5.4 points to 4.8. Then came the pandemic, which took every state down together.
Two lines on a chart are not an estimate. The rest of this document is about turning them into one: what Washington’s scores would have been without the McCleary money, and whether the difference is distinguishable from noise. The short answer is that it is not. But first it is worth being precise about what the court actually decided, because a lot of the public argument assumes it decided something it did not.
The Supreme Court gets to say what the constitution means, and nothing here disputes that. But it is worth reading what the court actually said, because the popular memory of McCleary is that the court found Washington’s children were being shortchanged and ordered the state to fix it. The opinion is narrower than that, in a way that matters for how the money should be judged.
The court defined the duty by inputs, not outcomes. The 2012 opinion (Washington Supreme Court 2012) built on a 1978 case, Seattle School District v. State (Washington Supreme Court 1978), which read “ample” to mean “liberal, unrestrained, without parsimony, fully, sufficient,” and read “education” as broad opportunity: preparing children to “compete adequately in our open political system, in the labor market, or in the market place of ideas.” McCleary affirmed the trial court’s gloss that ample means “considerably more than just adequate,” then stated its own holding in one sentence:
The “education” required under article IX, section 1 consists of the opportunity to obtain the knowledge and skills described in Seattle School District, ESHB 1209, and the EALRs. It does not reflect a right to a guaranteed educational outcome.
The court went further, noting “the inescapable truth that certain factors critical to a student’s achievement are simply outside the State’s control.” So to the question of whether McCleary rests on some assumption that every child starts equal and only money separates them: no. The court expressly declined to make results the standard. Its holding is about opportunity, and opportunity is measured in what the state provides.
The finding of underfunding was an accounting finding. The Legislature had defined its own “program of basic education.” The trial record showed the state’s allocation formulas paid districts less than that program actually cost: utilities funded at $115 per student against $252 actually spent, instructional salaries about $8,000 below what districts paid, and so on. Districts filled the gap with local levies. The court’s logic was that “full funding is whatever the Legislature says it is” amounts to “little more than a tautology,” and that levies, being subject to local votes and local property wealth, are not the “regular and dependable” revenue the constitution requires. That is the whole violation: the state was not paying the cost of the program it had itself defined, and was relying on an impermissible source to cover the difference.
Equity enters only through the levy analysis. The constitution’s phrase “without distinction or preference on account of race, color, caste, or sex” is recited in the opinion but never applied. The court’s equity concern was between districts: property-rich districts can raise more per levy dollar than property-poor ones. There is no analysis of racial or economic achievement gaps, and no WASL pass rate or graduation figure anywhere in the part of the opinion that finds the violation. The achievement statistics that do appear are quoted from legislative reports as background.
Compliance was judged the same way. From the 2014 contempt finding (Washington Supreme Court 2014) through the $100,000-a-day sanction (Washington Supreme Court 2015) to the order that ended the case (Washington Supreme Court 2018), the court “measured progress specifically according to the areas of basic education identified in ESHB 2261 and the implementation benchmarks established by SHB 2776”: transportation, materials and operating costs, all-day kindergarten, K–3 class size, and salaries. When it released the Legislature in June 2018, it did so because the state “has now complied with this court’s orders to fully implement the State’s new program of basic education,” while noting in the same paragraph that the plaintiffs “still dispute the constitutional adequacy of the funding formulas.” No outcome measure appears in any of the seven orders.
So the answer to the Times’s question, is Washington meeting its constitutional commitment, has a legal answer and a substantive one. The legal answer is yes, as of 2018, because the court defined the commitment as funding a statutory program and the program got funded. The court was candid that it had done nothing more: it “has not purported to take over public education” (Washington Supreme Court 2017). The substantive answer, the one the framers would have cared about and the one the court explicitly left to the Legislature and the public, is whether the children are better educated. That is what the rest of this document tries to measure.
Bazzaz’s own survey of outcomes is careful and, on achievement, muted. Washington performs slightly ahead of the nation in NAEP reading and roughly at the national average in math, with scores below pre-pandemic levels here as everywhere. The state’s own goal, 90% of students proficient on its state assessments, sits well above the roughly 70% at grade level in reading and two-thirds in math. Underneath the averages are sharp disparities: only 42% of Washington’s Latino fourth graders reach NAEP’s “basic” level in reading.
State superintendent Chris Reykdal frames the constitutional money as a floor rather than a program, and puts the open question plainly:
Money really does matter. But how you deploy it matters too.
That is the question this project takes up, with an explicit counterfactual rather than a before-and-after comparison. The narrowing matters. This analysis can say something about grade 8 mathematics, because NAEP provides a comparable measure across states. It cannot evaluate the two areas where Bazzaz finds Washington genuinely lagging: preschool access, where the state ranks 7th in per-child spending but 34th in enrollment, and postsecondary completion, where its six-year rate of 56.5% is among the nation’s worst. Both fall outside the constitutional guarantee as the court read it, and neither has outcome data that supports this design.
The National Assessment of Educational Progress — “The Nation’s Report Card” — is a federally administered test given to a representative sample of students in every state, not to every student (National Center for Education Statistics 2024). It is run by the National Center for Education Statistics in grades 4 and 8, in mathematics and reading, in odd-numbered years (the pandemic pushed the 2021 administration to 2022).
Three properties make it the only usable outcome here:
The outcome here is grade 8 mathematics. Grade 8 has the longest clean run of state-level results, and mathematics is more responsive to schooling — and less to home environment — than reading, which makes it the more sensible place to look for an effect of a school-funding change. Scale scores move slowly: differences of two or three points between states are small, and the gap the analysis is trying to detect is of that order.
Between the 2009–11 and 2019–21 biennia, Washington’s state spending on K–12 education rose 110%, while all other state spending rose 52% (Washington Research Council 2020). Over the same period the state’s standing on the National Assessment of Educational Progress did not improve relative to the rest of the country. In grade 8 mathematics Washington led the national public average by 5 points in 2003 and by 2 points in 2024.
Those two facts are usually deployed as a rhetorical pair, and the chart above invites exactly that reading. It should be resisted. Three things have to be settled before the money and the scores can be compared at all:
How much money actually reached schools per student? The 110% figure measures the state budget line. McCleary’s central mechanism was a levy swap — the state assumed obligations previously met by local levies — so some share of that growth is a change in who writes the check, not in how much is written. Using OSPI’s district accounting, the Washington Research Council reports that from SY 2010–11 to SY 2018–19 total per-pupil revenues rose 49.7%, state per-pupil revenues rose 81.6%, and local taxes per pupil fell 0.3% (Washington Research Council 2020).
The pipeline behind this document does not reproduce that last figure. It uses the Census F-33 survey rather than OSPI’s F-196, and over the same years F-33 puts Washington’s local revenue per pupil up 15.1%, with local property tax alone up 14.9% — not flat, and not falling. The two sources agree closely on the totals (F-33 gives +55.5% total and +86.0% state) and on the direction of the levy swap: state share of revenue rises about 12 points in F-33 (58.6% to 70.1%) and about 14 in OSPI (64.6% to 78.4%). They disagree on local revenue in sign, not just magnitude. The disagreement is not a definitional one about which local receipts count, and not a year-alignment artifact; both were checked. It is a genuine difference between two federal and state collections, and it is left visible here rather than resolved by picking the more convenient number. Nothing in the estimates below depends on it: the outcome model uses NAEP scores only, and the first stage uses total revenue, where the sources agree.
F-33 stops at 2020, but little happens after that. OSPI’s inflation-adjusted total for Washington’s K–12 revenue rose from $13.4 billion in 2012–13 to $20.2 billion in 2018–19, then only to $21.0 billion by 2024–25 (Superville 2026). Nearly 90% of the growth had arrived by the 2019 NAEP administration. Those are totals rather than per-pupil figures, but the timing is the point: 2019 is when the increase was complete, not a midpoint. NCES’s per-pupil spending series, charted in the same article, rose 49.1% from 2010–11 to 2018–19, a third source close to the Research Council’s 49.7%.
What were those dollars worth? Nominal per-pupil growth has to be deflated twice: once for inflation, once for the fact that Puget Sound labor got more expensive relative to the rest of the country over the same decade.
Compared to what? Washington’s post-2019 scores fell. So did everyone’s. The counterfactual is not “Washington in 2011”; it is “Washington had the legislature not responded to McCleary.”
This project answers the third question with a synthetic control, and carries the first two through the data pipeline so the resource measure being tested is one that a skeptic would accept.
panel |>
dplyr::summarise(
States = dplyr::n_distinct(state),
`NAEP years` = dplyr::n_distinct(year),
`First year` = min(year),
`Last year` = max(year),
Observations = dplyr::n()
)| States | NAEP years | First year | Last year | Observations |
|---|---|---|---|---|
| 50 | 11 | 2003 | 2024 | 550 |
Three sources, all public, all pulled by script:
| Source | Series | Access |
|---|---|---|
| NAEP Data Service (NCES) | State mean scale scores, grade 8 math | R/01_fetch_naep.R |
| Census F-33 / CCD via Urban Institute | Revenue and expenditure per pupil | R/02_fetch_finance.R |
| BEA Regional Price Parities; CPI-U | Place and time deflators | R/03_price_adjust.R |
Every API pull is validated against hand-transcribed published figures in data/cache/naep_verified_anchors.csv before the analysis runs (make test). This guards against the failure mode where an upstream schema change silently returns a different series and the analysis keeps running.
plot_spending(panel)
panel |>
dplyr::filter(state == TREAT_UNIT) |>
dplyr::transmute(
Year = year,
`Nominal $/pupil` = round(rev_pp),
`Real, cost-adj. $/pupil` = round(rev_pp_real),
`State share of revenue` = scales::percent(state_share, accuracy = 0.1)
)| Year | Nominal $/pupil | Real, cost-adj. $/pupil | State share of revenue |
|---|---|---|---|
| 2003 | 8610 | 11449 | 61.6% |
| 2005 | 9383 | 11756 | 60.9% |
| 2007 | 10874 | 12831 | 61.9% |
| 2009 | 11514 | 13112 | 58.2% |
| 2011 | 11437 | 12591 | 58.6% |
| 2013 | 12319 | 13192 | 60.1% |
| 2015 | 13782 | 14240 | 61.6% |
| 2017 | 15473 | 15077 | 63.7% |
| 2019 | 17780 | 16468 | 70.1% |
| 2022 | NA | NA | NA |
| 2024 | NA | NA | NA |
The obvious way to evaluate McCleary is to compare Washington before and after. That fails immediately, because 2022 and 2024 scores fell across the entire country. Any before-and-after comparison credits McCleary with a pandemic.
The next idea is to pick a comparison state. But no single state is a good match for Washington on demographics, economy, and prior test-score trajectory at once, and whichever one you pick, a skeptic can reasonably accuse you of having picked it to get the answer you wanted.
Synthetic control (Abadie et al. 2010) solves both problems by refusing to choose. Instead of one comparison state, it builds a weighted average of many, with the weights chosen by an explicit rule rather than by the analyst.
Synthetic Washington is a weighted average of other states’ NAEP scores, where the weights are picked so that the weighted average tracks Washington’s actual scores as closely as possible in the years before 2013.
Two constraints make it honest:
Concretely, the optimizer in this analysis lands on:
fits$score |>
tidysynth::grab_unit_weights() |>
dplyr::filter(weight > 0.001) |>
dplyr::arrange(dplyr::desc(weight)) |>
dplyr::transmute(State = unit, Weight = scales::percent(weight, accuracy = 0.1))| State | Weight |
|---|---|
| SD | 63.1% |
| AR | 14.9% |
| NE | 11.8% |
| MA | 3.3% |
| MT | 2.5% |
| MN | 1.0% |
| DE | 0.3% |
| WI | 0.2% |
| ID | 0.2% |
| OR | 0.2% |
| NH | 0.2% |
| FL | 0.2% |
| AZ | 0.1% |
| UT | 0.1% |
| IN | 0.1% |
| MO | 0.1% |
| GA | 0.1% |
| TN | 0.1% |
| VT | 0.1% |
Read that as: the mix of states whose combined grade 8 math path most closely reproduced Washington’s own path from 2003 through 2011. From 2013 onward, that same fixed mix is carried forward, and the difference between Washington and this synthetic Washington is the estimated effect.
The weights come from a constrained optimization, not from judgment. The procedure minimizes the distance between Washington and the weighted donor pool across a set of predictors — here, Washington’s NAEP score in each of the five pre-treatment years (2003, 2005, 2007, 2009, 2011) — subject to the non-negativity and sum-to-one constraints above. That is a quadratic program, solved numerically; tidysynth hands it to an interior-point solver.
Note what is not in the predictor list: per-pupil revenue. Money is the treatment mechanism, estimated separately below as a first stage, not something the donor pool is asked to match on. With only five pre-treatment periods, the predictor set cannot identify more than five predictors — adding spending terms on top of the five score lags makes the problem numerically singular. R/05_synth.R documents this at the point of decision.
Treatment is dated to 2013, the first NAEP administration after the January 2012 ruling. The money phased in through 2019, so the estimated effect is a dose that grows over the post-period rather than a clean step.
The donor pool excludes states with their own major finance-reform shocks in 2008–2022 — KS, NY, NJ, CT, PA, NM, TX, CA, MI, IL — which leaves 39 donors. A state that had its own court-ordered funding overhaul is not an untreated comparison. That exclusion list is the most contestable input in this analysis; notes/methodology.qmd reports how much it matters, and the short answer is: almost none.
With one treated unit there is no sampling distribution and no standard error in the usual sense. A gap of four points between Washington and its synthetic might be an effect, or might be the kind of wobble this method produces routinely. The only way to know is to find out what “routinely” looks like.
So the procedure is run again, pretending each donor state was the one treated in 2013. Nothing happened to Nebraska in 2013, so whatever gap the method produces for Nebraska is pure noise — a measure of how much apparent “effect” this design manufactures when there is nothing to find. Doing this for every donor gives a distribution of placebo gaps to judge Washington against.
Each unit is scored by its post/pre RMSPE ratio. RMSPE is root mean squared prediction error — the typical size of the gap between a state and its synthetic. Taking the ratio of the post-treatment value to the pre-treatment one normalizes for fit quality: a state the donor pool could never match well to begin with will have large gaps afterward for entirely uninteresting reasons, and dividing by its pre-period error discounts that.
Rank Washington among those ratios and you get a p-value directly: if Washington ranks k-th of N, then p = k / N. It answers the question “what fraction of states show a post-treatment divergence at least this large when nothing happened to them?” A Washington that sits unremarkably in the middle of the placebo pack is a Washington whose gap is indistinguishable from noise.
A finance reform that does not change real resources cannot be tested for effects on achievement. This is the check that the treatment exists.
plot_trends(
fits$money,
title = "Washington did buy something",
subtitle = "Real, cost-of-living-adjusted revenue per pupil against a synthetic control built from untreated states",
y_lab = "Revenue per pupil (2019 $, cost-adjusted)"
)
plot_trends(
fits$score,
title = "Observed and synthetic Washington",
subtitle = "Grade 8 mathematics mean scale score"
)
plot_gap(
fits$score,
title = "Estimated effect of the McCleary response on grade 8 math",
subtitle = "Positive values mean Washington outperformed its synthetic counterfactual"
)
plot_placebos(
fits$score,
title = "Washington's gap against every donor state's placebo gap",
subtitle = "If Washington's line is unremarkable inside the gray band, the estimate is indistinguishable from noise"
)
inf$table |> head(12)| unit_name | type | pre_mspe | post_mspe | mspe_ratio | rank | fishers_exact_pvalue | z_score |
|---|---|---|---|---|---|---|---|
| UT | Donor | 0.0503016 | 45.521593 | 904.97248 | 1 | 0.025 | 5.8896656 |
| AZ | Donor | 0.0892804 | 17.965780 | 201.22865 | 2 | 0.050 | 1.0305396 |
| ME | Donor | 0.0702341 | 11.142441 | 158.64723 | 3 | 0.075 | 0.7365285 |
| FL | Donor | 0.1473889 | 16.003259 | 108.57845 | 4 | 0.100 | 0.3908196 |
| DE | Donor | 0.3177860 | 25.642702 | 80.69172 | 5 | 0.125 | 0.1982706 |
| GA | Donor | 0.1291653 | 9.264943 | 71.72936 | 6 | 0.150 | 0.1363884 |
| OR | Donor | 0.6492202 | 40.095181 | 61.75899 | 7 | 0.175 | 0.0675462 |
| WI | Donor | 0.1771365 | 9.458450 | 53.39640 | 8 | 0.200 | 0.0098051 |
| NE | Donor | 0.5422149 | 28.803747 | 53.12238 | 9 | 0.225 | 0.0079131 |
| AK | Donor | 1.0059318 | 40.523646 | 40.28468 | 10 | 0.250 | -0.0807270 |
| VT | Donor | 0.3294292 | 12.238795 | 37.15152 | 11 | 0.275 | -0.1023605 |
| TN | Donor | 1.7065453 | 55.998266 | 32.81382 | 12 | 0.300 | -0.1323110 |
Washington’s post/pre RMSPE ratio is 3.72, ranking 33 of 40 units, giving a placebo-based p = 0.825.
Did Washington’s McCleary response buy measurable achievement? Not detectably — and the money did arrive, so that is a finding about the spending, not about missing data. But “not detectable” here includes the effect the research literature would have predicted, which is a weaker verdict than “no.”
Two results, and they point in different directions.
The money is real and large. By 2019 Washington was spending $3,065 more per pupil than its synthetic counterpart, in inflation- and cost-of-living-adjusted dollars — a divergence that ranks 4th of 40 units against placebo, with pre-treatment tracking inside $35. The common objection that McCleary was merely a levy swap, moving the same dollars from local to state ledgers, does not survive the correction. Real resources per student rose, substantially, relative to what would otherwise have happened. Dropping the cost-of-living adjustment, which partly nets out the teacher raises that made up most of the treatment, and deflating by CPI-U alone widens the 2019 gap to $4,348, so the cost-adjusted figure is the conservative one.
The achievement gain is absent. Washington’s grade 8 math scores diverge from synthetic Washington by an average of 3.15 scale points across the post-treatment period. The median untreated state diverges by 3.09 points, which is the same number to within a rounding error. Its post/pre RMSPE ratio ranks 33 of 40 (p = 0.825), and the result holds whether treatment is dated 2013, 2015, or 2017, and whether or not the donor exclusions are applied.
Reykdal’s own explanation for flat scores is that the money was not enough for the students who need it most, those in high-poverty communities, and he puts the remedy at another $1 billion a year. Braun’s is that the Learning Assistance Program, the state’s categorical money for struggling students, is not always used as intended (Superville 2026). Both are claims about who the money reached, and a statewide mean can hide exactly that. So the same synthetic control was rerun on two NAEP subgroup means for grade 8 math: Hispanic students (23% of Washington’s test-takers in 2019, the largest group after White students) and students eligible for the National School Lunch Program. Both series are checked against the published 2019 NCES state snapshots before use.
sub |>
dplyr::transmute(
Group = c(hispanic = "Hispanic", nslp = "Lunch-eligible")[label],
Donors = n_donors,
`Revenue gap 2019` = dollars(money_2019),
`Score gap 2019` = pts(gap_2019),
`Placebo rank` = paste(rank, "of", n_units),
`Detection floor` = sprintf("%.1f", detect_floor),
`Predicted (J&M)` = sprintf("%.1f", jm_pred_2019)
) |>
knitr::kable(align = "lrrrrrr")| Group | Donors | Revenue gap 2019 | Score gap 2019 | Placebo rank | Detection floor | Predicted (J&M) |
|---|---|---|---|---|---|---|
| Hispanic | 25 | $3,300 | -5.8 | 15 of 26 | 6.2 | 4.2 |
| Lunch-eligible | 39 | $3,100 | -1.0 | 28 of 40 | 4.9 | 3.9 |
Neither subgroup diverges. Hispanic students’ post-treatment gaps run +3.7, -0.3, +2.0, -5.8 points from 2013 to 2019, ranking 15 of 26 against placebo (p = 0.58). The 2019 shortfall is the largest in either series, but untreated states produce gaps that size routinely. Lunch-eligible students track their synthetic within two points throughout (+1.7, -0.2, -0.5, -1.0; rank 28 of 40).
This does not rescue either side, for the same reason as before. The detection floors (6.2 and 4.9 points) again sit above what the literature predicts (4.2 and 3.9). Subgroup means are noisier, and the Hispanic series loses 14 donor states to suppressed small-sample cells. The prediction is also, if anything, low, since the meta-analysis finds larger effects for low-income students. Two further limits apply:
What the subgroup runs do rule out is the strong form of the targeting argument: that the money produced a large, visible gain for disadvantaged students which the statewide average concealed. There is none at this resolution.
Bellevue’s Aramaki points to Mississippi, which spends less than Washington and has raised its NAEP reading scores (Superville 2026). That is a grade 4 reading story, and the analysis above is grade 8 math, so it cannot speak to it. The same design was rerun on grade 4 reading, the subject and grade where Mississippi’s gains are measured. Mississippi was dropped from the donor pool, since its reading reforms are a concurrent treatment of their own.
The result is the closest thing to a signal anywhere in this analysis, and it is still not one. Synthetic Washington tracks the real one tightly before 2013 (pre-period RMSPE 0.32 points), and the post-treatment gaps through 2019 run +0.4, +3.7, +0.7, -0.5. Washington ranks 4 of 39 against placebo (p = 0.10), because a good pre-period fit makes even a modest divergence stand out. But the divergence is a single 2015 bump that is gone by 2019, the year the money peaked, which is the opposite of what a funding effect should look like. The detection floor is 4.6 points against a literature prediction of 3.8.
Mississippi does not change the comparison either way. It carries 0.1% of the weight when allowed in the pool (synthetic Washington’s grade 4 reading is mostly Minnesota, at 78.0%), and with it included the rank is 6 of 40. Aramaki’s point is about policy, not money: a state that decided every child would read. The same Stanford–Harvard report that ranks Washington’s recovery lists it among ten states that had adopted fewer than seven of the “science of reading” policy elements by January 2024. None of the ten improved in reading from 2022 to 2025; Mississippi, with more, did (Dewey et al. 2026). Nothing here tests that. What it shows is that Washington’s added money did not buy a detectable reading gain.
It does settle the narrow question it was built for: after a large, court-forced, substantially uniform resource increase, Washington’s grade 8 mathematics performance did not diverge from comparable states by any amount this design can see. The treatment was delivered and the outcome did not move.
It cannot tell you whether money works in general. The best-identified evidence that school spending raises achievement comes from reforms that targeted low-income districts (Jackson et al. 2016; Lafortune et al. 2018). McCleary was substantially uniform, and the accompanying levy cap partly redistributed away from high-levy districts. A null for McCleary is consistent with progressive finance reform working elsewhere.
It cannot evaluate what Bazzaz identifies as Washington’s actual weak spots — preschool access and postsecondary completion (Bazzaz 2026), neither of which the constitutional guarantee covers. Those need a different design, and the outcome data for them is worse. One reading of all this is that the paramount-duty clause did exactly what the court interpreted it to require, funding K–12 to the point where additional dollars there buy little, while the parts of a child’s education with the weakest measured results are the parts the clause never reached.
Which returns to the question the Times series opened with. Whether Washington is meeting its constitutional commitment depends on what you take the commitment to be. If it is the one the court enforced, a funded statutory program, the state met it in 2018 and the question is closed. If it is the one the constitution’s authors seem to have had in mind, educated children, then the honest answer from the best comparable measure we have is that the largest school-funding increase in the state’s history has not yet produced evidence of it — though, on the evidence above, not proof of its absence either. The second installment of Educating Washington reaches the same impasse from the trend lines alone (Superville 2026). Looking at the students the money was meant to reach, above, does not break the impasse either: state-level subgroup means carry the same power problem. What could is district-level data, where the levy cap made the size of the increase vary from one district to the next.
make docker-build # pinned R + Quarto image
make all # fetch -> test -> renderSee notes/methodology.qmd for specification checks and README.md for the data-refresh cadence.