Does AI Improve Access to Justice?

There is a comfortable story about AI and access to justice. Roughly 92% of the substantial civil legal problems of low-income Americans get no or inadequate legal help.¹ Lawyers are scarce and expensive. AI is abundant and nearly free. Therefore AI closes the gap.

Every step in that argument is defensible. The conclusion still does not follow, and we now have enough evidence to say why.

The evidence assembled here points somewhere more uncomfortable than either the optimistic or the pessimistic version of this debate. It is not that AI produces bad legal information — increasingly it does not. It is that legal information is not the only, and may not be the binding, constraint once a litigant enters the system. The controlled interventions we found that supply information have increased procedural participation without producing detectable improvements in case outcomes. And representation — the intervention everyone assumes works — turns out to work conditionally, in ways suggesting that lawyers are not primarily delivering legal knowledge either.

Meanwhile, two studies of federal court records document the same pattern since generative AI became widely available: substantially more self-represented filing, without evidence of improved litigation outcomes.^23, 24

Methodology

How these sources were selected. We ran a structured — not a formal systematic-review-protocol — search across peer-reviewed journals, working-paper repositories, research-institution reports, court administrative data, and government statistics, for evidence meeting three criteria: (1) it measures an outcome, not a sentiment; (2) where it makes a causal claim, it uses a design capable of supporting one, or the source itself disclaims causal identification; (3) it is a primary source, or a faithful report of one that we traced back to the original.

We separate findings into four evidence tiers, marked throughout: primary source (government data, administrative records, original survey instruments), peer-reviewed research, working paper or preprint (not yet peer-reviewed), and program or advocacy report (typically no control group).

One further convention, which matters most in Parts 4 and 5: claims that go beyond what a cited study states are marked as interpretation. Everything else is a report of a source's own finding. Where we draw an inference the underlying authors did not draw, we say so and say why — and where an inference is one of several readings the data supports, we give the alternatives.

Two exclusions are worth stating. We excluded vendor benchmarks and vendor-published performance claims entirely; they appear nowhere in what follows. And we excluded program evaluations reporting only volume served, satisfaction, or forms filed. Not because those programs are unserious — because they do not answer the question. That exclusion removed a substantial majority of the published material we encountered.

Every figure in this article was verified against the primary document, in its current version, in August 2026. Where a working paper has been revised, we cite the current revision and say so. Where a widely circulated figure could not be traced to a primary source, we say that rather than repeating it — six such figures appear in Part 1. Where we quote from a published abstract rather than from body text, the source entry says so.

The funnel: what "improving access to justice" could mean

Almost every disagreement in this field is a disagreement about which stage of a funnel is being measured. Setting the funnel out first makes the rest of the evidence legible.

Problem → Recognition → Information → Action → Participation → Legal position → Disposition → Real-world outcome → Welfare

• Problem. A civil justice situation occurs.
• Recognition. The person identifies it as something the legal system addresses.
• Information. They learn what rules apply and what options exist.
• Action. They file, answer, or otherwise engage.
• Participation. They appear, respond to motions, meet deadlines.
• Legal position. They have a defense, a claim, or a bargaining chip that carries weight.
• Disposition. The case ends in a judgment, dismissal, or settlement.
• Real-world outcome. They keep the housing, avoid the garnishment, obtain the status.
• Welfare. They are better off, accounting for costs and any market response.

Representation, self-help materials, and AI are not stages — they are interventions that enter the funnel at different points and can only affect stages downstream of where they enter.

The funnel is an analytical decomposition, not a claim that every case passes through these stages in sequence. Information can produce recognition; a lawyer can produce both; leverage can determine a disposition before any hearing occurs. The stages are a vocabulary for asking what was measured, not a model of how cases proceed.

What "outcome" means in this article

The word does most of the work in this literature and is used for at least four different things. We distinguish them throughout:

• Procedural outcome — an answer filed, an appearance made, a deadline met. Stages 4–5.
• Legal outcome — a judgment, dismissal, settlement, possession order, or monetary recovery. Stage 7, also called a disposition.
• Real-world outcome — housing retained, garnishment avoided, status obtained. Stage 8.
• Welfare outcome — the real-world result net of costs, and of any market or institutional response. Stage 9.

Where a source says "outcome" without specifying, we say which of these it measured.

The pattern this article documents is that most claims about AI and access to justice are supported at stages 2 through 5, while the evidence that matters sits at stages 7 through 9. Movement at an early stage does not propagate automatically to a later one.

Part 1: The gap is real, and it is not shaped the way most people think

The headline number is sound. The Legal Services Corporation's 2022 Justice Gap study — a NORC AmeriSpeak probability-panel survey fielded 18 October to 4 December 2022, covering 2,003 adults at or below 125% of the federal poverty line plus 3,305 above it, alongside a four-week census of requests for help across LSC-funded organizations — found that low-income Americans get no or inadequate legal help for 92% of their substantial civil legal problems. LSC-funded organizations turn away 49% of eligible requests due to limited resources.¹ (Primary source. There is no 2025 or 2026 edition.)

Two more recent findings complicate the standard framing.

The gap is not confined to poverty. The State Bar of California's 2024 Justice Gap Study — over 6,000 respondents, fielded 8 August to 7 October 2024, published 2025 — found that between 72% and 75% of households in every income group experienced at least one civil legal problem, and that between 84% and 86% of civil legal problems in every income group received no or inadequate help.² (Primary source.) The income bands run from at-or-below 200% of the federal poverty line to above 120% of area median income. On the narrower substantial-impact measure the spread is wider and non-monotonic — 79%, 76%, 73%, 78% — which still supports the point.

One comparison to avoid, and we flag it because it is tempting: California's 85% is not comparable to LSC's 92%. LSC's figure covers substantial-impact problems; California's comparable substantial-impact figure is 77%. The 85% covers all civil legal problems. These are California figures, not national ones.

A legal right to counsel does not produce counsel. New York City has a statutory right to counsel in eviction proceedings. The NYC Comptroller's May 2025 report found the share of eligible tenants receiving full representation fell from 71% in the fourth quarter of FY2021 to 42% in the fourth quarter of FY2024, with a monthly low of 30% in March 2025; in the Bronx, from 81% to 31% over the same quarters.³ (Primary source — government oversight report.)

The methodology deserves a note, because it cuts both ways. The Comptroller counts only cases with two or more appearances, which excludes the fastest-disposed cases where representation is lowest. But it also marks an entire case as represented if counsel appeared at any single appearance. Both choices inflate the figure. True representation across all filed cases is plausibly lower than 42%.

Capacity, not entitlement, is the operative constraint.

Six numbers you will see cited that do not survive checking

This field has an unusually severe zombie-statistic problem. Anyone writing about it should know which numbers are contaminated — and in four of these six cases, the problem is worse than the standard correction suggests.

1. "86% of civil legal problems get inadequate or no help." This is LSC's 2017 figure.⁴ The 2022 figure is 92%.¹ The persistence of this number is not a media failure: LSC's own website currently presents the 2017 figures in the present tense with no date qualifier — "In the past year, 86% of the civil legal problems reported by low-income Americans received inadequate or no legal help."⁵ The institution that produced the replacement is still serving the original, undated.

2. "80% of the civil legal needs of the poor go unmet." LSC never published this figure. The 2009 report says "less than one in five low-income persons get the legal assistance they need."⁶ The 80% is a rounded restatement — and it rounds the wrong way, since "less than one in five" implies more than 80% unmet.

3. "One legal aid lawyer for every 10,000 low-income Americans." We could not trace this to any primary source, and it appears to be a denominator-swap artifact. The ABA's 2023 Profile of the Legal Profession reports roughly three civil legal aid lawyers per 10,000 people in poverty — about one per 3,333 — with a state range from about 1.1 per 10,000 in Mississippi and South Carolina to 7.2 in New York.⁷ The circulating figure appears to be the ABA's denominator with the numerator collapsed.

4. "Only 37% of immigrants have a lawyer; 14% of detained immigrants." These are 2007–2012 figures from Eagly and Shafer's 2015 study.⁹ The 2025 update by Eagly, Shafer and Moulton — analyzing nearly 8 million cases — puts representation in merits completions at 52% for 2013–2024.⁸ (Peer-reviewed research on government administrative data. The authors state: "while we continue to show robust and statistically significant correlations between representation and case outcomes, we do not argue that representation caused these results.") The genuinely alarming current figure is a different one: representation among pending cases fell from 47% in 2012 to 31% in 2024.⁸

5. "Self-representation exploded between 1992 and 2013." Engstrom and Engstrom show the endpoints are not comparable: the 1992 study excluded limited-jurisdiction and small-claims courts, which account for 45.1% of the 2013 sample (417,063 of 925,344 cases), and the two studies used opposite coding presumptions for whether a party counted as represented.¹⁰ The apparent explosion is at least partly a measurement artifact.

6. "90% of landlords have lawyers; 10% of tenants do." No national source exists. The most widely circulated version — "only 4% of tenants are represented nationwide, compared to 83% of landlords" — appears in the National Low Income Housing Coalition's Advocates' Guide with no citation or footnote.¹¹ Every variant we traced (90/10, 83/4, 81/3) is an uncited secondary assertion. There is no national eviction-representation census. Jurisdiction-specific data exists and should be cited in its place.

One more to handle carefully: LSC's press materials describe serving over 6 million Americans annually, while its own 2025 data book reports 1.8 million people helped in closed cases for 2024.¹² The larger figure appears to sweep in information-and-education contacts. LSC does not reconcile the two anywhere we located. We use the 1.8 million figure and characterize the difference as unreconciled rather than false.

Part 2: Does legal information change outcomes?

This is the question that matters most for AI, because information is most of what current consumer AI supplies. The evidence is thin, rigorous where it exists, and largely negative.

Arizona housing court, randomized field experiment. Bernal and Yuan conducted what they describe as "the first large-scale field experiment to provide self-help to tenants facing eviction," published as an advance article in the American Law and Economics Review on 14 January 2026. Their finding: "we find no evidence that our self-help reduced default or improved outcomes." More troubling, they report "suggestive evidence that our self-help may have led to worse legal outcomes for Hispanic tenants and tenants with corporate landlords."¹³ (Peer-reviewed research, advance article not yet assigned to a volume. The harm finding is characterized by the authors as suggestive. Quoted from the published abstract.)

Ohio debt collection, RCT, N=600. Danser and Greiner's 2024 Access to Justice Lab trial mailed a one-page information sheet and an answer form to unrepresented debt-collection defendants in Hamilton County Municipal Court, Ohio, with 300 cases per arm, enrolled March through December 2023. Every result was null. Of disposed cases, "a little under two-thirds received a default judgment, with no statistically significant difference between the conditions (P = 0.52)." Answers were filed in 31 cases in the information arm versus 20 in the control (P = 0.142); help-center support was accessed in 12 versus 6 (P = 0.25).¹⁴ (Primary source — research-institution final report of an RCT. Eighty-four cases were undisposed at analysis and excluded, so rates are over 516 disposed cases.)

Boston debt collection, RCT. The same lab's earlier Boston Municipal Court trial found mailed materials roughly doubled participation: answer rates of 24% in both treatment arms versus 13% for control, and appearance rates of 14% and 15.3% versus 7.5%. An elaborately behaviorally-designed version — adding a cartoon teaser postcard and prepaid postage to a letter, answer forms, pre-addressed envelopes, a courthouse map and a calendar reminder — did no better than the plain version.¹⁵ (Working paper.)

That last study is the one to watch, because of how it gets cited. Its outcomes were procedural — stage 5: whether the defendant filed an answer, and whether they attended the first hearing. The paper's own abstract says the mailings "roughly double the rate at which defendants participate in their lawsuits." Downstream advocacy citations routinely present it as evidence that self-help materials improve results. It does not show that.

The substitution is common enough to deserve a name.

Outcome substitution

Most published evaluations in access to justice report volume served, user satisfaction, self-reported understanding, or forms completed — procedural outcomes, stages 3 through 5. Whether someone kept their housing, avoided a judgment, or obtained the relief they sought is a legal or real-world outcome, stage 7 or 8.

When we restricted our search to studies measuring dispositions, the literature shrank dramatically — and the surviving studies mostly report nulls. The gap between how promising this field looks and how it performs is substantially a gap between what gets measured and what matters.

We are not exempt from this critique, and neither is anyone selling AI into this space. "Users report the tool helped them understand their case" is compatible with no change in whether they win.

Part 3: Does representation change outcomes?

Here we expected to find the clean contrast: information does nothing, lawyers work. The evidence is more interesting than that.

Memphis eviction RCT, N=1,140. Caspi and Rafkin randomized offers of legal representation to tenants facing eviction in Shelby County, Tennessee, in 2022–2023, offering a lawyer to 446 of 1,140 applicants. The instrumental-variables estimate — the effect on those who took up representation — was a 25 percentage point reduction in eviction judgments at 180 days, against a control mean of 68%.

But the study spans the expiration of federal emergency rental assistance, and the effect splits dramatically: −44 points while ERAP funds were available (s.e. 7.0, a 69% reduction from the control mean), attenuating to +6.1 points afterward (s.e. 6.3) — a change the authors describe as making lawyers' impacts "indistinguishable from zero." The difference between periods is significant at p<0.001. Lawyers secured roughly $2,100 in additional ERAP funding per client.

And on whether tenants actually moved: the intention-to-treat estimate is +0.8 percentage points (s.e. 2.6), against a control mean of 86%. The authors: "Lawyers do not have an economically or statistically significant impact on the probability a tenant moves."¹⁶ (Working paper, July 2026 revision. Note the estimands differ: the judgment effect is IV, the moving effect is ITT.)

New York City universal access, quasi-experimental. Cassidy and Currie exploited the staggered zip-code rollout of NYC's program across 727,692 eviction cases, published in the Journal of Public Economics (2023). In the published version, possessory judgments fell 32.1 points (s.e. 0.041) and warrant issuance fell 32.3 points (s.e. 0.037). Warrant execution — the point at which a tenant is actually removed — fell 8.4 points (s.e. 0.021), also significant at p<0.01.¹⁷ (Peer-reviewed research. Earlier NBER working-paper versions report materially different figures, including a null on warrant execution; the published estimates supersede them.)

That gradient is the finding. Representation moved the court record by roughly 32 points and actual removal by roughly 8 — about a four-to-one ratio between the legal outcome and the real-world outcome.

The effect on execution is larger in high-poverty areas (−12.6 points) and high-noncitizen areas (−10.8 points) than in their counterparts. Read alongside Memphis, where representation moved judgments substantially and moving not at all, the pattern is consistent: representation reliably changes what the court record says, and changes what happens to the person considerably less. Stage 7 moves more than stage 8.

The two Massachusetts trials. The most instructive pair in the literature comes from the same research team, same state, same period. In a Massachusetts District Court, full representation versus unbundled self-help moved the evictor's probability of obtaining possession from 62% to 34% (p=0.01), and rent waivers from 1.9 to 9.4 months (p=0.01), with N=129.¹⁸ In a Massachusetts Housing Court, full representation versus limited "lawyer for the day" assistance produced "no statistically significant evidence that the Provider's offer of full, as opposed to limited, representation had a large (or any) effect on any outcome of substantive import" — with N=184, and treated cases receiving 12.4 attorney-hours against 1.7 for the control, a ratio the authors describe as "over seven to one."¹⁹ (Peer-reviewed research and working paper respectively; the Housing Court study is under revise-and-resubmit.)

A detail that changes how the District Court result should be read: at least 70% of occupants in both arms attended two-to-three-hour instructional clinics, including help completing answer and discovery forms. This was not representation versus nothing. It was self-help versus self-help plus a lawyer — which is why the paper is titled The Limits of Unbundled Legal Assistance.

Any claim that "the RCTs show lawyers work" has to carry both trials. The authors offer two explanations for the divergence, each hedged. On intake: the District Court provider conducted individualized outreach and applied a "can we help here" screen, sending for randomization "only those cases for which it thought full representation would transform the outcome," while the Housing Court provider "employed no such screen." On litigation style: the District Court attorneys' "assertive or confrontational" approach contrasted with the Housing Court's "facilitative or nonconfrontational" one, which "may provide a partial explanation for the contrast in the results."

The counter-argument we are obliged to report. Collinson and colleagues analyze NYC's program at equilibrium rather than at the individual level, and estimate that listed rents rose $38.11 (95% CI 22.9–53.3) and $29.13 (95% CI 13.3–45.0) per month in the second year after rollout, depending on specification — a 1.2–1.6% price increase. First-year effects are much smaller: $12.51 (CI 1.3–23.8) and $6.47 (CI −6.5–19.4, including zero). They estimate tenant welfare decreases of $16.97–$25.68 per tenant per month.²⁰

Their own qualification is essential and we quote it: "While our point estimates of RTC's tenant welfare effect are always negative, 95% confidence intervals contain zero for high levels of tenant risk aversion and for a minority of the smaller and more noisily estimated robustness specifications of the rent effects." (2026 working paper, resubmitted to the American Economic Review, unrefereed. Bootstrapped standard errors on the welfare estimate are $7.63–$8.05.) We report it because omitting it would be exactly the selective citation this piece criticizes.

Part 4: So what is a lawyer actually providing?

If legal knowledge were the active ingredient, representation would work consistently and information would work partially. Neither is true.

The meta-analysis most directly relevant to this question — Sandefur, American Sociological Review (2015) — reaches the conclusion that organizes everything above:

"For the types of cases researched to date, knowledge of substantive law explains surprisingly little of lawyers' advantage compared to lay people appearing unrepresented."²¹

Her account of what lawyers do supply: "lawyers' impact is greatest when they assist in navigating relatively simple (to lawyers) procedures and where their relational expertise helps courts follow their own rules." (Peer-reviewed research, combining meta-analysis with nonparametric bounding to handle selection into representation. Her operative distinction is between substantive and relational expertise.)

Two scope notes. The opening qualifier — "for the types of cases researched to date" — is Sandefur's and matters. And this is not the most recent synthesis in the field: Caspi and Rafkin's 2026 eviction paper contains its own six-site Bayesian meta-analysis of right-to-counsel effects, pooling their Memphis trial with five earlier studies.¹⁶ What we did not find is a more recent comprehensive synthesis across civil case types; the post-2015 syntheses we located are either domain-specific or outside civil justice.

The Memphis result puts a concrete number on the same idea, and the mechanism is the authors' own: "Lawyers and rental assistance serve as complements because financial resources can be useful bargaining chips, and lawyers can help parties access resources."¹⁶

Their framing is complementarity, not substitution, and they test the strong version and reject it: controlling for ERAP take-up explains only about 30–50% of the pre/post gap. They attribute part of the remainder to ERAP's mere existence changing landlord behavior, and note that social workers with access to the same funds did not produce comparable effects — which cuts against a pure-money story. They also document value beyond housing outcomes: tenants valued lawyers well above provision cost even when final outcomes did not change, citing delay, reduced stress, and "the chance to exercise voice in the legal system."

Interpretation: we read the Memphis, Massachusetts and New York results together as pointing to leverage — money to settle with, procedural power, a counterparty obliged to deal with you — rather than legal knowledge as what moves outcomes. Legal knowledge is an input to deploying leverage, not a substitute for having it. Each study supports a piece of this; none states it in this form, and Sandefur's qualifier about case types applies here too.

This is the sense in which "does AI improve access to justice" is mis-posed. The consumer-facing AI systems studied here primarily provide information, interpretation, and drafting assistance. Where information is not the binding constraint, better information should not be expected to close the gap — and, as it turns out, has not.

The important qualification: this is a claim about the systems that have been studied, not about what AI can do in principle. Issue spotting, procedural triage, and defect detection are all things current models can attempt, and all of them would generate leverage rather than information. None has been evaluated on outcomes. Part 6 returns to this.

A bottleneck further upstream — and what may have happened to it

One more finding belongs here, and its date matters more than its sample.

Sandefur's Community Needs and Services Study surveyed 668 residents of a midwestern city of approximately 350,000–450,000 people, in 60–90 minute in-person interviews during the summer and fall of 2013. Two-thirds (66%) reported experiencing at least one of twelve categories of civil justice situation in the previous 18 months. Asked to characterize those situations from a multi-select list — including bad luck or part of life, moral, private, criminal, part of God's plan, legal, social, bureaucratic, and family or community — residents characterized 9% of their civil justice situations as legal, and 4% as criminal. 56% were described as bad luck, part of life, or part of God's plan.

Just over a fifth (22%) of situations were handled with the assistance of a third party from outside the person's social network. Where no advice was sought, the most common reason given was not seeing the need (46% of such instances), followed by believing it would make no difference (24%); cost played a role in 17%.²² (Peer-reviewed academic research. Note the denominators: 9% and 22% are shares of situations, not of people, and the characterization item allowed multiple selections.)

On that evidence, a major failure mode as of 2013 was stage 2: problem non-recognition. It occurred before anyone went looking for information or a lawyer, and neither intervention could reach it.

The fieldwork was conducted in 2013. That is not a footnote. It predates smartphone saturation as a legal-help channel, the growth of informal legal advice communities online, and the existence of systems that let someone describe a situation in plain language and be told it might be an illegal eviction. Describing a problem and having it named is precisely a recognition assist, and it is the task current AI is best at in this entire domain. We should not assume the 9% figure describes 2026.

That cuts against using this study as a current description of the bottleneck. It also suggests a different reading of the recent data.

If recognition improved, we would expect more people identifying that they have a claim and acting on it — movement from stage 2 into stages 3 and 4. That is what the federal court data shows: self-represented filings rose from roughly 11% to 17% of non-prisoner civil filings, with self-represented parties accounting for 59% of the growth in civil filings.²³ Interpretation: the pro se surge may be partial evidence that the recognition bottleneck loosened.

And stages 7 and 8 did not move. Dismissals rose; wins stayed under 1%.^23, 24

If that reading is right, it strengthens rather than weakens the argument of this section: one constraint was relieved, and another was waiting behind it. Recognition was necessary and not sufficient. What people gained was entry into a process — not the leverage to prevail in it.

We hold this reading loosely. Nobody has measured recognition rates before and after generative AI, and the alternative explanation for the surge — that people who already knew they had a claim simply found filing cheaper — fits the data equally well. Distinguishing the two is a study someone should run.

We also note what would count as a replication and does not exist. No national US survey has replicated the CNSS characterization instrument. LSC's 2022 study measures something adjacent but distinct — whether respondents believed a lawyer could help, finding they "did not know if a lawyer could help resolve 74% of their problems"¹ — which is perceived professional utility, not problem characterization. The World Justice Project's 2019 US General Population Poll is the nearest national measure of whether people perceive their problems as legal.

Part 5: What has measurably changed since generative AI

Shah and Levy (MIT/USC, working paper, March 2026) analyzed more than 4.5 million non-prisoner federal civil cases from the Federal Judicial Center Integrated Database covering FY2005–FY2026, alongside PACER docket metadata and a stratified sample of 1,600 federal civil complaints — 200 per year, 2019–2026 — run through commercial AI-text detection. Findings:

• Pro se share of non-prisoner filings held at a long-term steady state of roughly 11%, rising to 16.8% in FY2025
• Pro se filings accounted for 59% of the growth in civil filings
• Docket entries per pro se case rose from 16.9 to 23.3, up 38% — these litigants are more active, not merely more numerous
• Judicial dismissals rose from roughly 60% to 63%
• Pro se wins "remain rare throughout (under 1%)"
• AI-generated text detected in complaints: 0.1% before 2023, an aggregate 8.2% after, reaching 18.0% in early 2026²³

(Working paper, not peer-reviewed. The authors explicitly disclaim causal identification: "We do not claim to identify a causal effect of GPT-4 on pro se filing, only that the observed time series is difficult to rationalize without generative AI playing a role." The detector's published error rates were benchmarked on non-legal text, not federal complaints.)

Cohen-Sasson (working paper, revised 1 August 2026) analyzed approximately 2.8 million federal civil filings for FY2008–2025 using stylometric indicators of AI-assisted drafting — sentence-length variability, AI-marker density, and moving-average type-token ratio. The current version reports that the pro se plaintiff rate, "roughly 11%… has doubled to 22.3% in three years," and that AI-flagged complaints are "dismissed more often, terminated earlier, and no more likely to prevail than their AI-unassisted counterparts."²⁴ (Working paper, not peer-reviewed, no accepted placement. Stylometric detection is inferential and error-prone.)

How independent are these two? Less than the convergence suggests, and this is worth stating plainly. Both draw on the same underlying records — the Federal Judicial Center Integrated Database — with Cohen-Sasson's window a subset of Shah and Levy's. Their agreement on the pro se trend is the same measurement on the same data, and their matching ~11% baselines are a consistency check on data handling rather than corroboration.

What is independent is the AI-detection layer: a commercial neural detector applied to 1,600 sampled complaints versus a homegrown stylometric measure applied to roughly 13,000. Those approaches are unrelated, and they produce substantially different prevalence estimates on different populations. The finding they jointly support — that AI-assisted filings do not win more often — rests on two genuinely different detection methods applied to a shared case universe.

The shape echoes Part 2. Mailed self-help doubled participation in Boston and changed no dispositions; the national data shows participation rising and dispositions not following. Whether the two share a mechanism is untested.

Why AI-assisted filings might do worse, not merely no better

A randomized trial by Schwarcz and colleagues, published in the Journal of Law and Empirical Analysis (2026), had 137 law students complete legal tasks with and without AI assistance — 125 completed all six — blind-graded on a seven-point scale. Overall quality improved significantly. Broken down by attribute, the gains concentrated in professionalism and clarity, with improvements ranging from +0.42 to +0.95 and +0.46 to +0.60 across the two tools tested. In aggregate, neither tool produced a statistically significant accuracy gain (+0.01 and +0.09).²⁵ (Peer-reviewed research. Law students, not litigants; October 2024 fieldwork with tools since superseded. At the individual task level accuracy gains were significant for one of six tasks, both tools, p<0.01. The authors disclose the multiple-comparison issue in their task-level tables.)

One plausible mechanism follows, and we state it as a hypothesis rather than a finding: AI may make a filing appear more professionally presented without proportionately improving its legal accuracy. If judges respond to presentation while still detecting substantive defects, then an AI-assisted filing that reads like a lawyer wrote it — and contains a defect a lawyer would not have made — could be disposed of faster than an obviously amateur filing a judge reads charitably.

The observed pattern of AI-flagged complaints being dismissed more often and earlier is consistent with that hypothesis. It is also consistent with several others, including that the people newly filing pro se have weaker claims than those who filed before. Nothing in the evidence reviewed here distinguishes between them, and the law-student trial cannot: it measured graded work quality, not judicial response.

On hallucination rates

We are deliberately brief here, because these numbers age faster than any other class of evidence in this article.

The structural findings are durable: error rates rise as cases become less prominent, and models "systematically overestimate their confidence relative to their actual rate of hallucination."²⁶ The most access-relevant study we found built its dataset from posts by ordinary people seeking legal guidance on Reddit — rewritten by the researchers into short scenarios — and found hallucination rates of 0.45 in Los Angeles, 0.55 in London, and 0.61 in Sydney, across housing, employment, family, and criminal/traffic matters.²⁷ (Preprint. n=100; late-2024 model snapshots; the authors expect higher rates in smaller jurisdictions.)

Every specific rate in this literature was measured on models one to three years old and should not be quoted as current performance. The point that survives is narrower and more useful: accuracy on lay-phrased questions about local law has been substantially worse than accuracy on lawyer-phrased questions about federal cases — and local-law questions dominate the justice gap.

One wrinkle for anyone assuming monotonic improvement. A 2026 Princeton benchmark tracking eight ChatGPT generations across more than 8,000 verified citations found citation hallucination fell to 1.23% with the August 2024 GPT-4o release and then rose to 6.57% with GPT-5.1 — a bootstrapped p=0.001.²⁸ (Preprint.) Newer is not automatically safer.

Part 6: What would have to be true for AI to close the gap

Taking the evidence seriously, AI would close the access gap if at least one of the following were true. Each is testable, and none has been tested.

1. AI supplies leverage, not just information. A system that reliably identifies a defect in a debt-collection plaintiff's standing, or an uncured habitability violation, is not delivering information — it is manufacturing negotiating leverage where none existed. The Memphis complementarity result suggests this is the mechanism that matters. Nobody has measured whether AI can do it.

2. AI changes institutional behavior rather than litigant behavior. The Massachusetts and Memphis results both point to the counterparty and the forum as decisive. AI deployed on the court's side — triage, error detection, notice redesign — may do more than AI deployed on the litigant's side. There are practice reports here and, as far as we found, no controlled evaluations.

3. AI solves recognition rather than resolution. If problem non-recognition remains a major bottleneck, the highest-leverage intervention is helping someone realize they have a legal problem at all — a task AI is unusually well-suited to. This is not an untried idea so much as an unmeasured one: consumer chatbots are already performing recognition assistance at enormous volume, informally and outside any evaluation framework. Nobody has measured whether recognition rates changed, or whether recognition without leverage improves anything downstream.

4. Scale substitutes for effect size. A small per-case effect delivered to millions could exceed a large effect delivered to thousands. This is the strongest version of the optimistic case, and it depends entirely on the per-case effect being greater than zero. Current measurements do not establish that it is.

What the evidence supports

Stated as boundaries, in both directions.

Supported by the evidence reviewed here:

• Self-represented filing in US federal courts has increased substantially since generative AI became widely available.^23, 24
• There is no current evidence that this increase has translated into higher pro se win rates.^23, 24
• Information-only interventions can increase procedural outcomes without improving legal outcomes.^{13, 14, 15}
• Legal representation can materially improve legal outcomes in some settings.^17, 18
• The effect of representation depends heavily on complementary resources and institutional context.^16, 19
• Representation moves recorded dispositions substantially more than it moves real-world outcomes — by roughly four to one in the one study measuring both with precision.¹⁷
• No randomized trial has established that generative AI improves case outcomes for self-represented litigants.

Not established by the evidence reviewed here:

• That AI caused the increase in pro se litigation. Both studies disclaim causal identification, and both draw on the same case records.
• That AI generally harms self-represented litigants.
• That AI cannot improve access to justice.
• That AI cannot improve legal problem recognition.
• That AI can substitute for legal representation.
• That AI improves or worsens outcomes across civil litigation generally. The causal evidence base is overwhelmingly eviction and debt collection.

The study we could not find

Our search surfaced no randomized trial of AI assistance delivered to self-represented litigants with measured case outcomes.

What exists instead: a field study of 91 legal aid staff measuring self-reported productivity, with no independent quality assessment and no client outcomes;²⁹ a randomized trial on law students;²⁵ and two observational federal-court time series drawing on shared data.^23, 24 The question the entire debate turns on has not been subjected to the method that could answer it.

The study is not exotic. It requires: a defined population of unrepresented litigants in a single case type; random assignment to an AI-assisted intake and drafting tool versus the status quo; a rubric written and registered before scoring; and dispositions — not satisfaction, not forms filed — as the primary outcome, with failure modes and subgroup effects reported alongside the headline number, including where the tool did worse.

That last requirement is not incidental. Bernal and Yuan found suggestive evidence that a self-help intervention harmed the most vulnerable participants.¹³ A study designed only to detect benefit would have missed it.

The relevant experiment has not yet been run. We intend to run it. The protocol, data, and results — including a negative result — will be published here.

Summary of evidence

Limitations

Domain concentration. Nearly all rigorous causal evidence on representation comes from eviction and housing, with debt collection second. Generalizing to civil legal representation as a category is not supported by these studies.

No systematic review protocol. Our search was structured but not a registered systematic review. A different search could surface studies we missed.

Age of the AI evidence. Every capability measurement cited here was taken on models between one and three years old. Structural findings are more durable than rates.

The two studies of AI-era pro se litigation share a data source. Both draw on the Federal Judicial Center Integrated Database; only their detection methods are independent. Neither is peer-reviewed, and both are live documents subject to revision. This is the most important empirical claim in the article and it carries the weakest publication status.

One load-bearing source predates the technology under discussion. Sandefur's 2013 characterization finding comes from a single city, n=668, and has never been replicated nationally. We treat it as a historical baseline rather than a current measurement, and Part 4 sets out why the mechanism may have changed.

We could not verify six commonly cited figures, listed in Part 1, and have excluded them.

Every figure in this article was verified against the primary source in its current version in August 2026. Cooperative publishes applied AI research, including negative and inconclusive results. Corrections to any figure are welcome and will be published.

References

1. Legal Services Corporation (2022). "The Justice Gap: The Unmet Civil Legal Needs of Low-income Americans." NORC AmeriSpeak probability panel fielded Oct–Dec 2022; 2,003 adults at or below 125% FPL plus 3,305 above, and a four-week intake census across LSC grantees.
2. State Bar of California (2025). "The 2024 California Justice Gap Study." Over 6,000 respondents, fielded 8 Aug – 7 Oct 2024. California only; the substantial-impact figure is 77%, not directly comparable to LSC's national 92%.
3. Office of the New York City Comptroller (2025). "Evictions Up, Representation Down." Housing court administrative data. Figures are fourth-quarter snapshots. Counts cases with two or more appearances, and marks a case represented if counsel appeared at any one of them.
4. Legal Services Corporation (2017). "The Justice Gap: Measuring the Unmet Civil Legal Needs of Low-income Americans." Source of the superseded 86% figure.
5. Legal Services Corporation. "Unmet Need for Legal Aid." Retrieved August 2026; presents 2017 figures in the present tense without a date qualifier.
6. Legal Services Corporation (2009). "Documenting the Justice Gap in America." States "less than one in five low-income persons get the legal assistance they need" — the source behind the circulating 80% figure, which LSC never published.
7. American Bar Association (2023). "ABA Profile of the Legal Profession." Reports approximately three civil legal aid lawyers per 10,000 people in poverty.
8. Eagly, I. V., Shafer, S., & Moulton, R. (2025). "Access to Counsel in Immigration Court, Revisited." Iowa Law Review, 111(1). Approximately 8 million cases, 2013–2024. The authors explicitly decline to claim representation caused the outcome differences they observe.
9. Eagly, I. V., & Shafer, S. (2015). "A National Study of Access to Counsel in Immigration Court." University of Pennsylvania Law Review, 164(1). Source of the widely-cited 37% and 14% figures, covering 2007–2012.
10. Engstrom, N. F., & Engstrom, D. F. (2024). "The Making of the A2J Crisis." Stanford Law Review Online. Methodological critique of the standard self-representation trend claim.
11. National Low Income Housing Coalition. Advocates' Guide. Source of the "4% of tenants / 83% of landlords" formulation, published without citation.
12. Legal Services Corporation (2025). "By the Numbers" (2024 data). Reports 1.8 million people helped in closed cases.
13. Bernal, D. W., & Yuan, A. Y. (2026). "The Limits of Self-help: A Field Experiment in an Arizona Housing Court." American Law and Economics Review, advance article published 14 January 2026. Quoted from the published abstract.
14. Danser, R. L., & Greiner, D. J. (2024). "Final Report: Avoiding Default and Asserting Affirmative Defenses in Debt Collection Matters." Access to Justice Lab, Harvard Law School. RCT, N=600, Hamilton County Municipal Court, Ohio.
15. Greiner, D. J., & Matthews, A. (2015). "The Problem of Default, Part I." Boston Municipal Court RCT, working paper. Outcomes are procedural — answer filing and appearance — not dispositions.
16. Caspi, A., & Rafkin, C. (2026). "Legal Assistance for Evictions." Working paper, July 2026 revision. RCT, N=1,140, Shelby County, Tennessee. Also contains a six-site Bayesian meta-analysis of right-to-counsel effects.
17. Cassidy, M. T., & Currie, J. (2023). "The Effects of Legal Representation on Tenant Outcomes in Housing Court: Evidence from New York City's Universal Access Program." Journal of Public Economics, 222, 104844. Staggered zip-code rollout, 727,692 cases. Figures here are from the published version; earlier NBER working-paper estimates differ materially and are superseded.
18. Greiner, D. J., Pattanayak, C. W., & Hennessy, J. P. (2013). "The Limits of Unbundled Legal Assistance." Harvard Law Review, 126, 901. RCT, N=129. At least 70% of occupants in both arms attended instructional clinics, making this self-help versus self-help plus representation.
19. Greiner, D. J., Pattanayak, C. W., & Hennessy, J. P. (2012). "How Effective Are Limited Legal Assistance Programs? A Randomized Experiment in a Massachusetts Housing Court." RCT, N=184. Null result; working paper under revise-and-resubmit. Read alongside source 18, which it conflicts with.
20. Collinson, R., Humphries, J. E., Kestelman, S., Nelson, S., van Dijk, W., & Waldinger, D. (2026). "Equilibrium Effects of Eviction Protections: The Case of Legal Assistance." Working paper, resubmitted to the American Economic Review, unrefereed. Included as counter-evidence; the authors note their welfare confidence intervals contain zero under some assumptions.
21. Sandefur, R. L. (2015). "Elements of Professional Expertise: Understanding Relational and Substantive Expertise through Lawyers' Impact." American Sociological Review, 80(5), 909–933. Combines meta-analysis with nonparametric bounding. Quoted from the published abstract.
22. Sandefur, R. L. (2014). "Accessing Justice in the Contemporary USA: Findings from the Community Needs and Services Study." American Bar Foundation. n=668, one midwestern city, fieldwork summer–fall 2013. Percentages cited are shares of situations, not of respondents; the characterization item was multi-select.
23. Shah, A. V., & Levy, J. Y. (2026). "Access to Justice in the Age of AI: Evidence from U.S. Federal Courts." Working paper, March 2026, not peer-reviewed. 4.5M+ non-prisoner federal civil cases. The authors explicitly disclaim causal identification.
24. Cohen-Sasson, O. (2026). "Artificial Access to Justice: AI and the Surge in Pro Se Litigation." Working paper, revised 1 August 2026, not peer-reviewed, no accepted placement. Supersedes the earlier preprint titled The New Pro Se. Shares its underlying data source with source 23.
25. Schwarcz, D., Manning, S., Prescott, J. J., Barry, P., Cleveland, D. R., & Rich, B. (2026). "AI-Powered Lawyering." Journal of Law & Empirical Analysis, 3(1), 220–250. RCT, 137 law students (125 completed all six tasks), October 2024 fieldwork.
26. Dahl, M., Magesh, V., Suzgun, M., & Ho, D. E. (2024). "Large Legal Fictions: Profiling Legal Hallucinations in Large Language Models." Journal of Legal Analysis, 16, 64–93. Cited for its structural findings; the specific rates were measured on late-2023 models and are superseded.
27. Curran, D., Sporne, V., Frermann, L., & Paterson, J. (2025). "Place Matters: Comparing LLM Hallucination Rates for Place-Based Legal Queries." Preprint. Scenarios were derived from Reddit legal-advice posts and rewritten by the researchers. n=100; late-2024 model snapshots.
28. Liu, P., Stammbach, D., & Henderson, P. (2026). "Who Checks the Citations? Benchmarking Legal Hallucination Detection." Preprint. Longitudinal audit of eight ChatGPT generations, over 8,000 citations verified.
29. Chien, C. V., & Kim, M. (2025). "Generative AI and Legal Aid: Results from a Field Study and 100 Use Cases to Bridge the Access to Justice Gap." Loyola of Los Angeles Law Review, 57, 903. n=91 legal aid staff. Outcomes are self-reported productivity, not client outcomes or independently assessed work quality.