Needs more than a quick edit8 of 12 checks passed
The output contains arithmetic errors in the weekly and segment lifts that would require re-checking before use. A PM could not rely on it without verifying the numbers.
Output
Recommendation: don’t ship on Monday. The reported ~6% lift is reproducible, but it includes a treatment-specific tracking incident. The supplied aggregates also cannot establish significance for the pre-registered, user-level metric. We have a promising signal—not a reliable launch decision.
What the raw data shows
I summed orders and daily user counts across the 28 days:
| Arm | Sum of daily users | Logged orders | Orders / summed users |
|---|---|---|---|
| --- | ---: | ---: | ---: |
| Control | 196,373 | 16,560 | 0.08433 |
| Treatment | 226,652 | 20,234 | 0.08927 |
The calculation is:
\[ \text{Lift}=\frac{20,234/226,652}{16,560/196,373}-1=5.86\%. \]
So Zoe’s arithmetic is right for this aggregate ratio. However, summed daily users are not necessarily unique randomized users. If people appear on multiple days, this is orders per user-day, not the pre-registered orders per user over the test.
The tracking incident materially changes the result
On 14 October, treatment recorded 1,354 orders versus 604 in control, with 8,107 versus 7,026 daily users. Treatment’s order rate was almost twice its normal level. That is consistent with the documented duplicate-event incident.
As a sensitivity check only, removing that entire day from both arms gives:
| Arm | Sum of daily users | Logged orders | Orders / summed users |
|---|---|---|---|
| --- | ---: | ---: | ---: |
| Control | 189,347 | 15,956 | 0.08427 |
| Treatment | 218,545 | 18,880 | 0.08639 |
\[ \text{Lift excluding 14 October} =\frac{18,880/218,545}{15,956/189,347}-1 =2.52\%. \]
The remaining signal is positive, but much smaller. Dropping a whole day is not a valid substitute for recovering actual orders: the incident lasted nine hours, and that day also contains legitimate transactions.
The effect is not stable or broad-based
Using the same aggregate calculation:
| Week | All-user lift |
|---|---|
| --- | ---: |
| 1 | +5.58% |
| 2 | +2.68% |
| 3 | +0.23% |
| 4, as logged | +15.07% |
| 4, excluding 14 October | +1.38% |
Excluding the incident day, the full-period lift is +11.9% for new users and −0.14% for returning users. New-user weekly lifts decline from approximately 24.0% to 15.0%, 4.7%, and 2.5%.
That suggests the remaining aggregate gain is concentrated among new users and may be fading. It does not prove novelty: calendar effects, changing cohorts, or instrumentation could also explain the pattern. Nor does a positive new-user estimate alone establish a statistically reliable difference between segments.
What we cannot conclude yet
“Significant” is not established by these files. For the intended user-randomized analysis, we need unique assigned users—including users with zero orders—and each user’s deduplicated order count. Daily aggregates do not provide the user-level variance or account for repeated appearances. Treating user-days as independent could overstate precision.
The denominator needs investigation. Treatment has 15.4% more summed daily users than control, despite the planned 50/50 assignment, with an imbalance throughout the test. This is a warning, not proof of assignment failure: if these are active users, treatment could change activity. Check assignment counts separately from exposure/activity counts. An activity-conditioned denominator can change the estimand and introduce bias.
AOV is slightly down, not flat. Weekly declines range from approximately 0.2% to 0.6%, all within the 2% guardrail. Weighting the reported weekly averages by logged order counts gives approximately $48.25 control versus $48.01 treatment, or −0.51%. That is descriptively reassuring, but duplicate orders may distort the weights or AOV calculation. These summaries also lack uncertainty estimates.
What we should do next
- Reconcile against canonical transactions. Deduplicate using order IDs and validate the incident’s actual scope rather than assuming only treatment was affected.
- Audit randomization and denominators. Check unique assignments, eligibility, exposure logging, missing users, and sample-ratio mismatch.
- Recompute the pre-registered analysis: intention-to-treat orders per unique assigned user over the full 28 days, with user-level confidence intervals; recompute AOV from valid orders and revenue.
- Apply the original decision rule to that repaired result. If lift is positive and significant and the AOV guardrail passes, shipping becomes defensible. If trustworthy recovery is impossible, rerun with fixed instrumentation and a pre-specified duration and analysis.
- Investigate durability and targeting separately. Pre-specify new/returning-user interactions and time-since-exposure analyses in follow-up work. Don’t use this post-hoc segment result to justify a targeted launch.
Bottom line: pause the launch, repair the measurement, and decide on the registered metric—not the contaminated headline.
Claims the judge couldn’t find in the brief
- Week 2 lift is +2.68%.
- Excluding the incident day, the full-period lift is −0.14% for returning users.
- New-user weekly lifts decline from approximately 24.0% to 15.0%, 4.7%, and 2.5%.
Grades and run details
Decision model 83 · LLM judge 62
Decision model checks
- failUses the supplied evidence correctly39%
- passAddresses the actual decision97%
- passRespects explicit constraints49%
- passIdentifies material uncertainty94%
- passAvoids unsupported claims37%
- passProduces the required deliverable49%
- passCatches the sample ratio mismatch66%
- passRemoves the bug day100%
- passReads the trend and who it helps91%
- passTrusts the data before reading it99%
- failGets the base of every number right53%
- passDoesn't overread an unclear result57%
Run
- Run
- #1
- API response time
- 72 s
- Submitted
- 6 Oct 2026