Experiments I'd run next

The mechanism. Mental Accounting says money doesn't sit in one undifferentiated pool in people's heads. It gets sorted into labelled accounts, and a labelled account is protected in a way an unlabelled one isn't. Salience does the actual labelling work, and not by being more memorable in the abstract, but by contrast: a name you can picture (“Save for Phone”) stands out against the generic, interchangeable rows around it (“Savings Pocket 2,” “Everyday Account”), much like one bold number jumping off an otherwise plain bill.

Already tested. The high school field session tested the labelling half of this live, with paper envelopes and a room of Year 8/9 students, and watched $30 accumulate in the “save” envelopes that nobody consciously decided to save.

This experiment. It tests the contrast half directly: does a name that stands out in a list of accounts protect a balance as well as a name that stood out on a hand-labelled envelope did?

Prompting a customer to name a new savings pocket at the moment they open it, rather than defaulting to an auto-generated label, will reduce the share of that pocket's balance withdrawn to zero within 90 days, without adding enough friction to meaningfully hurt onboarding completion.

Illustrative, not real product data. Assume 30% of customers who open a second savings pocket withdraw its full balance within 90 days, the generically-labelled pocket behaving less like “savings” and more like a second everyday-spend account with extra taps.

The study. Buell and Choi ran a real field experiment inside CBA's credit card acquisition funnel: showing each card's drawbacks as prominently as its perks, a “Good and the Bad” page, instead of benefits-only marketing, left take-up statistically unchanged, but improved which card people picked. Customers who saw the downsides went on to spend 9.9% more, cancel 20.5% less, and miss fewer payments. The full teardown, with the real numbers, is on this site's Tradeoff Transparency page.

The gap. That experiment tested tradeoff transparency within one product category: comparing credit cards to each other. It didn't test the comparison one level up: credit card against the other ways the same customer could finance the same purchase, like a personal loan or a Buy Now, Pay Later plan, today sold on entirely separate pages, by entirely separate teams, with no drawbacks ever shown against each other at all.

Showing a customer's actual financing options, credit card, personal loan, BNPL, side by side, with each one's real drawbacks named as plainly as its benefits, will shift some customers towards the option that actually fits how they intend to use it. Take-up itself shouldn't move: CBA's within-category version changed which card people picked without changing how many applied, and this is that same mechanism working one level up.

Illustrative, not disclosed CBA data. Assume 8% of applicants who land in today's credit-card-only funnel end up choosing a personal loan or BNPL plan instead, entirely on their own initiative. The funnel never surfaces either as an alternative, so this only happens when someone already knew to go looking for one.

The line. Making a financing alternative visible for the first time isn't a neutral change, so the line is worth stating before the design, not after. This isn't built to talk anyone out of a credit card. For plenty of customers, revolving credit is the right tool.

The restraint. The design only surfaces the other real options before the commitment: inform the decision, don't engineer it, exactly the restraint the original CBA study held to. See Not Testing Is Still a Bet for the fuller case for that line.

The study. Halperin, Ho, List and Muir ran this at real scale on 1.5 million Uber riders who'd just had a late ride: a $5 coupon apology paid for itself, restoring future spend that a generic “sorry” alone didn't: a costly signal doing work a free one can't, the mechanism this site documents as Reciprocity.

The sharper finding. Their paper also found a result worth designing around from the start: sending the identical coupon again after a second bad ride backfired. Riders spent less than if Uber had said nothing at all. The authors' own explanation: an apology reads as a promise, and reusing the exact same one a second time reads as that promise already broken. The full teardown, with the real numbers, is in the Voltage Effect field session.

After a service failure, a costly and specific apology, a fee credit plus a plain explanation of what happened, will outperform a generic scripted apology on post-incident satisfaction. Because the same research found that reusing an apology verbatim can backfire on a repeat failure, the design should also test, as a secondary branch rather than the headline result, whether varying the apology's content and framing protects that advantage where a fixed script wouldn't.

Illustrative, not real support-desk data. Assume post-incident CSAT (1–5) currently averages 3.1 after a generic apology message, standard deviation 1.1, typical for a scripted, one-size response with no real cost attached.

The study. Thorndike's finding, in one sentence: a rater who forms a strong impression on one visible trait unconsciously extends that same judgment to other traits of the same target they haven't actually evaluated, see Halo Effect for the full study. Thorndike, and later Nisbett & Wilson, tested that at the level of a single person's traits: one instructor's warmth colouring judgment of his unchanged accent and mannerisms.

The gap. This experiment tests the identical mechanism one level up: a single brand's channels, not a single person's traits. The bank in this scenario has never offered a digital home loan before; every application has gone through a broker or a branch appointment. It's about to launch a fully digital application: pre-approval in an afternoon, no paperwork mailed anywhere. Nothing else about the bank changes on launch day: the branch process, the broker relationships, the underwriting, the call centre, all identical to the day before.

The prediction. If the halo effect operates here the way it operates on a single rated person, simply being aware the bank now has one excellent digital channel should lift trust, and further lift application intent, in the channels that didn't change at all.

The hypothesis. Customers exposed to messaging about the bank's new digital home loan capability, regardless of whether they ever open it, will show higher intent to get a home loan with the bank through any channel, digital or not, than a matched group with no exposure. That's the headline, general claim: mere awareness of one excellent channel lifts trust in the whole relationship.

What's separate. Whether customers who go on to actually use the digital channel show an even larger lift is tested separately, as a secondary, non-randomised read (see Sub-branch), not folded into this headline number.

Illustrative, not real/disclosed data. Assume 6% of existing customers who are in the market for a home loan in a given quarter say they'd seriously consider getting it with this bank, through any channel, before the digital product launches or any awareness messaging goes out.

The risk. A halo is, by definition, trust extended to something nobody actually checked. That's the whole risk here: if awareness of the digital channel lifts intent to apply through the branch or a broker, and those channels haven't been resourced to match the promise the digital product makes, the bank ends up converting people on a trust it hasn't earned in the channel they actually use.

The guardrail. This experiment is not licence to under-invest in non-digital application support because the digital halo is doing the persuading, see Not Testing Is Still a Bet. The guardrails below exist specifically to catch that failure mode before it reaches a customer.

The study. Lacetera, Pope and Sydnor's finding, in one sentence: a number's leftmost digit dominates how its magnitude gets judged, so a real difference that crosses a leading-digit boundary, 39,999 miles to 40,000, $2.99 to $3.00, produces a disproportionately large shift in perceived value, even though the actual gap is tiny. Their evidence is 22 million real used-car sales; Thomas & Morwitz's lab work found the identical pattern in ordinary prices.

The gap. Neither tested an interest rate. This experiment moves the same mechanism onto a home loan's headline number. A rate advertised at 5.99% p.a. and one advertised at 6.00% p.a. cost a borrower almost exactly the same in real repayments, but the leading digit differs: 5.99% reads as “5% something,” while 6.00% reads as “6%” outright.

The prediction. If the mechanism holds here the way it holds for a car's odometer, 5.99% should be judged, and chosen, as meaningfully cheaper than 6.00%, disproportionate to the real cost difference between them.

A home loan advertised at 5.99% p.a. will be perceived as, and will convert to more started applications than, an otherwise identical loan advertised at 6.00% p.a., even though the two rates are set close enough that the real difference in monthly repayment is trivial.

Illustrative, not real/disclosed data. Assume 4% of visitors to the rate page who are shown a 6.00% p.a. headline rate go on to start an application within the same session.

Already standard. This experiment doesn't invent a new practice. .99 rate framing is already standard, legal advertising across the lending industry, and the real cost stays disclosed via the comparison rate regardless of which headline number is shown.

What's being tested. How much that convention alone moves behaviour, so the bank can decide, with real numbers, whether to keep leaning on it as-is, cap how far it leans, or counter it by surfacing the comparison rate more prominently. See Not Testing Is Still a Bet for why measuring this honestly beats assuming it's fine because everyone already does it.

The studies. Bankwest's real Interesting Rates promotion pays every Easy Saver customer a genuinely competitive 5.75% p.a. everyday rate, then draws 50 winners a month for an 11.50% p.a. rate on top. Probability Weighting is the direct mechanism: a small, real chance of the better rate gets weighted in people's minds far past its true odds.

Two further findings shape how hard that weighting bites. Rottenstreich and Hsee (2001) found people overweight a small chance of something emotionally vivid even more than an equally small chance of a plain cash amount of the same value. That's exactly why a fast-food deal advertises “free food for life” instead of its cash value. A year of 0% interest on a real mortgage is at least as vivid a prize as free food, arguably more so: it converts directly into a large, concrete, easy-to-picture sum. Burger et al. (2020) found a second, separate effect: simply holding a lottery-style entry measurably lifts happiness before the draw resolves, win or not. A home loan application is normally a stressful, multi-week wait. A live entry gives an applicant something hopeful to hold onto during it, a genuinely different benefit from the conversion lift Probability Weighting alone would predict.

The gap. Classic prize-linked savings research, like Filiz-Ozbay, Guryan, Hyndman, Kearney and Ozbay's 2015 study, tests a real substitution: part of a saver's own guaranteed return is swapped for lottery expected value. Bankwest's promotion doesn't do that; its 5.75% rate exists whether or not anyone enters the draw. A home loan version pairing an already-competitive guaranteed discount with a separate chance at 0% sits further still from that substitution: no part of the applicant's real rate funds the prize. This tests Probability Weighting's own pull, not the prize-linked-savings trade-off.

This experiment. It tests whether advertising a genuinely competitive guaranteed discount alongside a separate, real chance at 0% p.a. for 12 months increases application starts on a new home loan rate page, against advertising the identical guaranteed discount alone, with that guaranteed rate held exactly constant between arms. It also checks a second, distinct prediction: that simply holding a live entry changes how applicants feel during the underwriting wait, not just whether they start applying.

Visitors shown the guaranteed discount plus a chance at 0% p.a. for 12 months start more applications within 7 days than visitors shown the identical guaranteed discount with no draw attached, even though the guaranteed rate on offer never changes between arms. Independent of that conversion lift, applicants in the treatment arm report less stress and higher satisfaction during the underwriting wait than applicants in the control arm, the same anticipatory-happiness effect Burger et al. found in lottery ticket-holders, whether or not they end up winning the draw.

Illustrative, not real/disclosed data. Assume 8% of visitors to the new home loan rate page start an application within 7 days when the page advertises the guaranteed discount alone.

The guardrail. The guaranteed discount has to be genuinely competitive against the rate the bank would otherwise offer that same applicant, not a rate quietly held back elsewhere to help fund the draw, and it must stay identical in both arms so the draw is the only variable under test. The odds, the number of winners, and the exact prize, 0% p.a. for 12 months on a capped loan amount, need disclosing as plainly as the guaranteed rate itself.

What's being tested. Whether a real, cited effect helps a genuinely competitive offer reach more of the people it's meant for, not whether a draw's excitement can be tuned to pull applicants into borrowing more than they can service. Loan size and serviceability assessment run identically in both arms, and a guardrail metric below checks that directly. See Not Testing Is Still a Bet.

The study. Kahneman, Knetsch and Thaler's finding, in one sentence: an identical price increase is judged fair when it's framed as protecting the seller's existing profit from a real cost increase, and unfair when it looks like exploiting a shift in demand or bargaining power. The number itself doesn't decide the verdict, the story behind it does. Their evidence is a telephone survey of Toronto and Vancouver residents judging realistic vignettes, including a hardware store that raised snow-shovel prices the morning after a storm (rated unfair by roughly 82% of respondents) and a landlord charging existing versus new tenants differently for the same unit.

The gap. Those vignettes measured stated opinions about a hypothetical price change, not real behaviour in response to a real one, and none of them tested a financial-services fee or rate notice specifically, where the cost being passed on (funding costs, compliance costs) is far less visible to a customer than a snowstorm is.

The prediction. If the same dual-entitlement logic holds here, a bank that names the real cost driver behind a fee or rate increase should see the change land as fairer, and, unlike KKT's survey, this experiment can check whether that shows up in real behaviour, not just a nicer opinion: fewer support contacts, fewer customers leaving.

Customers who receive a fee or interest-rate increase notice that names a real, verifiable cost driver will be less likely to contact support to question or dispute the change, and more likely to rate it as fair, than customers who receive an otherwise identical notice stating only the new number, even though the actual new fee or rate is unchanged between the two groups.

Illustrative, not real/disclosed data. Assume 18% of customers who receive a bare fee-increase notice, new amount only, no explanation, contact support to question or dispute the change within 30 days.

The guardrail. This mechanism only works honestly when the disclosed cost driver is real and verifiable, a genuine rise in funding costs, compliance costs, or similar, that the bank could substantiate if asked. Citing a vague or invented cost story to manufacture a feeling of fairness would be deceptive framing, not disclosure, and is explicitly out of scope for this experiment.

What's being tested. Only whether naming a true cost driver changes how a genuine, already-decided fee change lands, not whether that framing can be used to justify an increase that wouldn't otherwise be defensible on its own. See Not Testing Is Still a Bet for why measuring this honestly matters more than assuming good framing is harmless.

The mechanism. Payment Transparency says a purchase's felt cost depends on whether the payment method makes you rehearse the amount and whether the money leaves immediately. The Credit Card Premium is the sharpest real case of it: bidders told they'd pay by credit bid close to double what cash-instructed bidders bid, for the identical tickets, because credit strips out both cues.

Already suggested, not yet tested. Both principle articles' own “Where it can help” sections argue the same two cues can be put back deliberately, a running balance shown at the moment of tap, a receipt that totals spend by category, but neither study tested whether simply telling someone the mechanism, in plain language, changes what they actually spend. That's a different, weaker intervention than redesigning the interface itself: it relies on a customer remembering and acting on a fact, not a changed screen.

This experiment. It tests whether education alone, no interface change, no restricted product, moves real spending, and whether it matters when that education arrives: repeated, close to the moment of use, or delivered once, before any spending has happened at all.

Customers told the payment-transparency heuristic in plain language spend less on their lowest-transparency linked payment method (a stored or linked credit card) over the following months than customers told nothing. The reduction is larger and more durable for customers who receive the heuristic repeatedly, as a contextual in-app message near the moment of spending, than for customers who receive it once, as onboarding content before they've made a single transaction, because the underlying mechanism, rehearsal and immediacy, is about what's salient at the moment of paying, not what was once explained in the abstract.

Illustrative, not real/disclosed data. Assume customers in the control arm spend an average of $780 a month on their lowest-transparency linked payment method in the 90 days after opening a new debit account, with a standard deviation of $360 reflecting how unevenly card spending is actually distributed across a customer base.

The guardrail. The message has to state the real mechanism honestly, something like “paying by credit doesn't feel like spending right away, which is part of why people spend more on it,” not a shame-based or fear-based framing, and it has to apply the same way regardless of a customer's income or existing balance, so it reads as financial literacy, not a judgment about who's trusted to spend.

What's being tested. Whether informing someone of a real, cited mechanism changes their own behaviour once they know it, not whether the message can be tuned to manipulate spending in either direction. See Not Testing Is Still a Bet for why measuring this honestly matters more than assuming a well-meaning message is automatically harmless.

The study. Pseudo-Set Framing showed that grouping arbitrary items into a visible "set" makes people push to complete it, even when the reward doesn't change, even when finishing costs something, and even when people are told the grouping is made up. The effect held across five separate studies, gambling, effort, giving, and purchasing, not just one narrow task.

The gap. None of the paper's studies tested a real product's own multi-step setup flow, the exact place a bank, telco, or insurer already asks customers to complete several small, genuinely useful tasks (verify ID, link a funding source, add a beneficiary, set a goal) with no shared visual frame tying them together.

This experiment. It tests whether picturing those same required steps as wedges of one circle to complete, rather than an ordinary checklist, increases how many customers finish all of them, without changing what's actually required or adding a single extra step.

New customers shown their remaining setup steps as wedges of one "complete your profile" circle finish all required steps within 14 days at a higher rate than customers shown the identical steps as a plain checklist, even though the number of steps, the effort each takes, and the reward for finishing are all unchanged between arms.

Illustrative, not real/disclosed data. Assume 41% of new customers complete all 4 required setup steps (ID verification, linked funding source, a named beneficiary, a savings goal) within 14 days of opening an account under the existing plain-checklist flow.

The guardrail. Every wedge in the circle has to correspond to a step that's genuinely required or genuinely useful to the customer, none added purely to round the set out or make the shape more compelling. The circle can't be blocked or nagged into completion with dark patterns, delayed access to core banking functions, repeated interstitials, that go beyond what the ordinary checklist arm also uses.

What's being tested. Whether a real, cited completion mechanism helps customers finish setup steps they already need to do, not whether the visual can be tuned to pressure people into rushing through steps they'd otherwise have skipped for a good reason. See Not Testing Is Still a Bet.

The studies. A controlled lab experiment found participants offered a lottery-style bonus deferred payment more often than participants offered a guaranteed bonus of the identical expected value, with the pull strongest among low-balance participants. Michigan's real-world Save to Win programme moved $8.56 million into new accounts in its first year using the same structure.

The gap. Neither study is a live digital-product test: the lab experiment paid a one-off lab bonus, and Save to Win is a whole account type, not a feature layered onto an existing one. No test yet isolates the payout-structure swap alone, inside one already-existing digital savings product, with everything else held constant.

This experiment. It tests whether replacing part of an existing savings feature's guaranteed bonus rate with a prize-draw of equal expected value, inside the same app, for the same customers, increases net new deposits, without changing anything else about the product.

Customers offered a prize-draw bonus structure, funded from the identical pool that would otherwise pay a guaranteed rate bump, deposit more into the dedicated savings feature over 60 days than customers offered the guaranteed rate bump directly, even though the total expected payout is the same in both arms. The gap is largest among customers with the lowest starting balances, matching the lab study's own finding.

Illustrative, not real/disclosed data. Assume customers in the guaranteed-rate control arm deposit an average of $310 in net new funds into the dedicated savings feature over 60 days, with a standard deviation of $410 reflecting how unevenly savings deposits are actually distributed.

The guardrail. The prize pool must be funded from the exact amount that would otherwise be paid as guaranteed interest, never as an added cost that makes the product worse in expectation, and the deposit itself must never be at risk regardless of the draw's outcome. Odds and expected value have to be disclosed as plainly as an interest rate would be, not buried under excitement-focused copy.

What's being tested. Whether a real, cited payout-structure effect helps customers save more of their own money, not whether the framing can be tuned to pressure the specific low-balance customers it appeals to most into depositing more than they can afford. See Not Testing Is Still a Bet.

The study. Kivetz, Urminsky and Zheng found effort and motivation increase the closer someone perceives themselves to be to a finish line, and that perceived proximity alone, not real distance, drives it: a 12-stamp card with 2 stamps already filled in accelerated purchasing identically to a genuinely shorter 10-stamp card, even though both needed exactly 10 more purchases. The principle's own “where it can help” case is a genuine progress bar showing someone how close they actually are to finishing a form.

The gap. The principle proposes this; nobody has tested it. A home loan appointment booking flow is exactly the kind of long, multi-step form (contact details, loan and property details, a preferred meeting type, a time slot) where abandonment is common and a completion cue has never been isolated as the only variable.

This experiment. It tests two different applications of that mechanism on the same flow: showing an honest step count at the flow's natural, coarse chunking, and re-chunking the identical real work into more, still-genuine steps so a customer sits further through the count at the same real point, the exact lever the original study's 12-stamp card used against a 10-stamp one.

Visitors shown a real step-progress indicator, at either chunking, complete and confirm a booking at a higher rate than visitors shown the identical flow with no progress indicator, even though the fields required and the appointment options offered are unchanged in every arm. The study's mechanism runs on how close someone feels, not how far they actually have left, so splitting the same real work into more granular genuine steps, a customer sitting further through the count at an identical real point, produces a larger lift than an honest step count at the flow's natural, coarser chunking.

Illustrative, not real/disclosed data. Assume 34% of visitors who start the appointment booking flow complete all 4 steps and confirm a booking under the existing no-progress-indicator flow.

The guardrail. The step count and progress bar have to reflect the real number of steps and real position in the flow at every screen, never compressed or re-ordered to make the remaining effort look smaller than it is. The total step count should be visible from the very first screen, not revealed one step at a time, so no one commits to step one without knowing there are three, or five, more behind it.

Re-chunking has a real/fake line. Splitting a step into finer sub-steps is only legitimate when each resulting step is still genuinely distinct, required content, contact details and identity verification are two real things, not one field split in half to manufacture an extra step. No step shown, at either chunking, may be fabricated, reordered to hide what's left, or padded purely to inflate the count.

What's being tested. Whether an honest completion cue helps people follow through on a booking they already want to make, not whether the count can be tuned to disguise how long the form actually takes. See Not Testing Is Still a Bet.

The study. Save More Tomorrow let employees commit today to a contribution-rate increase that wouldn't take effect until their next scheduled pay raise, so take-home pay never actually shrank on the day it changed. Of 162 employees who'd just declined an immediate increase, 78% accepted the deferred version instead, and average savings rates rose from 3.5% to 13.6% of pay over four raises, about 40 months, with 78% still enrolled at the end.

The gap. Every tested version of this relies on an employer who knows the exact date and size of the next raise in advance. A savings or banking app has no such schedule to work from: the best it can do is notice, after the fact, that a customer's regular salary deposit just got bigger.

The prediction. If the mechanism is really about timing the ask against a gain instead of a felt cut, the source of the raise shouldn't matter, scheduled or detected, only that the increase is committed to in advance and only takes effect once the extra money has already arrived.

Customers offered a one-tap commitment to increase their auto-save rate at their next detected pay rise, instead of being asked to increase it immediately, accept some increase to their savings rate at a higher rate than customers asked to increase it right now, even though the amount of the increase on offer is identical in both arms.

Illustrative, not real product data. Assume 9% of customers shown an in-app prompt to increase their auto-save rate by 2% right now accept it.

The risk. A jump in a bank deposit isn't always a raise. A one-off bonus, a tax refund, or a new but temporary higher-paying gig would all look identical to a real, ongoing pay rise the moment it lands, and treating any of them as permanent would auto-escalate someone's savings against income that's about to disappear.

The guardrail. A detected increase should hold across at least two consecutive pay cycles before it triggers the commitment, and any triggered increase must be reversible with one tap and refundable in full for a short window afterwards, not just cancellable going forward. Getting the timing wrong should cost the customer nothing.

What's being tested. Whether committing in advance, against a gain instead of a felt cut, is what drives acceptance, not whether raise-detection can be tuned to trigger more often than it should. See Not Testing Is Still a Bet.

The mechanism. Not Enough Choice found reactance is triggered specifically by an active removal, not by an option simply never being available, and its own “where it can help” section claims plainly that explaining the reason should defuse it.

The gap. That claim has never actually been tested on a real removal notice. Nobody has isolated the explanation itself as the only variable.

This experiment. Both arms get the identical removal, on the identical timeline, with the identical balance migration. Only whether a reason is given differs.

Customers told why a feature is being removed contact support or lodge a complaint about it at a lower rate than customers told only that it's being removed, even though the outcome for their money is identical in both arms.

Illustrative, not real product data. Assume 22% of customers who receive a plain “this feature is going away” notice contact support or complain about it within 30 days.

The guardrail. Balance migration must be identical, immediate, and lossless in both arms. Nothing about a customer's money may differ based on which notice they happened to receive.

The line. The reason given in the treatment notice has to be the real, actual reason the feature is being retired, not a plausible-sounding cover story invented to test messaging. See Not Testing Is Still a Bet.

The study. Guéguen and Pascual's real street experiment found adding “but you are free to accept or to refuse” to an identical request for bus fare raised compliance from about 10% to about 47.5%.

The gap. That test was a single, low-stakes, in-person cash request. Nobody has tested whether the same freedom-naming line moves a digital, repeatable financial decision.

This experiment. It tests the identical mechanism on a real in-app ask: turning on round-up savings, a genuinely optional feature that's easy to feel nagged into.

Customers shown an in-app prompt to turn on round-up savings that explicitly names their freedom to decline accept it at a higher rate than customers shown the identical prompt without that line.

Illustrative, not real product data. Assume 11% of customers shown a plain round-up savings prompt turn it on.

The study. Hammock and Brehm's founding reactance experiment found that actively restricting an option makes it more wanted, not just less available, the same lever plenty of marketing already leans on informally.

The gap. Nobody on this site has tested that lever as an honest upsell mechanism, one where the restriction named is real, not manufactured urgency.

This experiment. It tests whether naming a real, existing eligibility gate increases interest in upgrading, without inventing a scarcity that isn't there.

Standard-tier customers shown a premium-tier message that names a genuine eligibility restriction click through to check their eligibility at a higher rate than customers shown the identical benefits with no restriction framing.

Illustrative, not real product data. Assume 6% of standard-tier customers shown a plain premium-benefits message click through to “see if you qualify.”

The risk. A restriction that reads as real but isn't invites exactly the manufactured urgency this site's own Scarcity and Signpost Effect articles warn against.

The guardrail. The message may only state a restriction that's true at the moment it's shown: a real, current eligibility gate or a genuinely limited rollout, never a fabricated headcount or a countdown with no real deadline behind it.

What's being tested. Whether naming a real restriction changes interest, not whether a restriction can be invented to manufacture demand. See Not Testing Is Still a Bet.

The study. Khan and Dhar had people first imagine committing to volunteer work, then choose between a pair of jeans and a vacuum cleaner of equal price. Imagining the virtuous act pushed choice towards the jeans, the indulgent option, compared with people who imagined no such act first. A second study found the same shift towards luxury sunglasses over practical ones.

The gap. Both studies used an imagined, hypothetical virtuous act in a lab setting. Nothing on this site has tested whether a real, completed responsible action inside a live product changes a real choice made minutes later.

The prediction. If the mechanism is a genuine temporary boost to feeling like a responsible person, it shouldn't matter that the virtuous act here is financial (setting up an extra loan repayment) rather than social (volunteering): a real completed action should shift a real redemption choice the same way an imagined one shifted a hypothetical one.

Customers who have just set up an automatic extra repayment on their credit card, then reach a reward-points redemption screen offering a practical option (a statement credit) and an indulgent option (a dining or travel voucher) of equal point value, choose the indulgent option more often than customers who reach the identical redemption screen without having just taken that action.

Illustrative, not real product data. Assume 35% of customers reaching the redemption screen without a prior prompt choose the indulgent voucher over the statement credit.

The risk. This experiment measures a real effect on real spending choices. If treated carelessly, the same finding could be misread as licence to engineer a virtuous moment purely to sell more discretionary redemptions, which would work against the customer's own financial interest.

The guardrail. The responsible action being measured, the extra repayment opt-in, has to already exist as a genuinely useful feature offered on its own merits, not one invented or timed to manufacture the licensing effect. Both redemption options stay equally visible and equally easy to pick in every arm, and a guardrail metric tracks whether the extra repayment itself is cancelled again soon after, which would signal it was ticked as a box rather than adopted.

What's being tested. Whether completing a responsible action shifts a later, unrelated choice, not whether the responsible-action prompt itself can be tuned to appear more often than it should. See Not Testing Is Still a Bet.

The study. Read and van Leeuwen had office workers choose a snack for the following week, either fruit or junk food, at two different points: a week ahead of time, or on the day itself. Choosing a week ahead, hunger made almost no difference to the choice. Choosing on the day, hungry workers picked junk food far more often than workers who'd just eaten, even though everyone was choosing the exact same two snacks.

The gap. The study's reward is food. Nothing on this site has tested whether the same advance-versus-in-the-moment reversal shows up when the reward is money someone could spend right now instead of saving.

The prediction. If the mechanism is really about how steeply a reward's value drops once "now" is on the table, it shouldn't matter that the choice here is a savings percentage instead of a snack: a commitment made a week before a bonus or refund lands should favour saving more than the identical choice made once the money is actually sitting in the account.

Customers who choose what share of an upcoming bonus or tax refund to transfer to savings a week before it lands commit a higher average percentage than customers who make the identical choice on the day the money actually arrives.

Illustrative, not real product data. Assume customers choosing on the day the money lands commit an average of 15% of it to savings.

The risk. Locking someone into a savings commitment made a week before the money arrives could work against them if their circumstances change in that week, an unexpected bill, a job loss, an emergency, that makes the earlier number wrong by the time it would apply.

The guardrail. This only runs on customers who've already opted into a windfall-savings feature on its own merits, and the advance commitment stays editable or fully cancellable right up to the moment the money lands, with one tap and no penalty. Getting the timing wrong should cost the customer nothing.

What's being tested. Whether the timing of the ask changes the commitment, not whether advance commitments can be made harder to reverse. See Not Testing Is Still a Bet.

The study. Arkes and Blumer's real field experiment found that theatergoers who paid full price for a season of plays attended more of it than theatergoers given the identical season at a random discount. Continued spending tracked what had already been spent, not what the season was actually worth going forward.

The gap. That study measured attendance after the sunk cost had already been paid. Nobody on this site has tested whether actively reminding someone of their own sunk cost, at the exact moment they'd otherwise consider switching, changes what they do next.

This experiment. It tests whether showing a customer their real, year-to-date spend on a plan, right on the renewal screen, reduces how often they check a cheaper alternative before renewing.

Customers shown their own cumulative spend on the current plan at renewal click "compare other plans" less often than customers shown an identical renewal screen with no spend figure, even though the same cheaper plan is available to both.

Illustrative, not real product data. Assume 22% of customers shown a plain renewal screen click "compare other plans" before renewing.

The risk. This tests a lever that could just as easily be used to trap customers on a worse deal by exploiting the same fallacy the Sunk Cost Fallacy article warns about.

The guardrail. The figure shown must be the customer's own real, verifiable spend, never rounded up or estimated in the company's favour, and the "compare other plans" option must stay exactly as visible and functional in both arms. Nothing about switching may get harder; only what's shown alongside the choice changes.

What's being tested. Whether showing a true sunk-cost figure changes behaviour on its own, not whether comparison shopping should be made harder. A result confirming the effect is a reason to avoid shipping this pattern, not a reason to ship it. See Not Testing Is Still a Bet.

The study. Gourville's lab studies found that restating a cost as a small daily amount, instead of one aggregate total, changed which other expenses it got compared against, and increased agreement to pay it.

The gap. Gourville's studies pitted the daily framing against the total, not alongside it. Most real checkouts that use a daily-equivalent price disclose the real total too, for legal and trust reasons, so whether the effect survives full disclosure is a live, untested question.

This experiment. It tests whether adding a truthful daily-equivalent figure next to the real annual total, changing nothing else about what's disclosed, still shifts more customers towards the annual plan.

Customers shown "33¢/day, billed annually at $120" select the annual plan over the identical monthly alternative more often than customers shown "$120/year" alone, with the true total visible in both arms.

Illustrative, not real product data. Assume 18% of customers choose the annual plan over the monthly plan when shown the plain annual total.

The risk. A daily-equivalent figure that isn't a true, correctly rounded division of the real total would mislead, exactly the failure mode the Temporal Reframing article names as the dishonest version of this lever.

The guardrail. The daily figure must be the exact annual total divided by 365, rounded normally, and the annual total must appear in the same type size, not fine print. Nothing about the monthly plan's price or visibility changes between arms.

What's being tested. Whether a fully disclosed daily reframe still moves choice, not whether disclosure can be minimised to make the reframe work harder. See Not Testing Is Still a Bet.

The study. Yadav and Monroe found that an additional discount stated directly on a combined bundle price carried more weight in perceived transaction value than the identical dollar amount split across the bundle's individual items.

The gap. The original study tested this with described purchase scenarios for physical goods. Nobody on this site has tested whether the same framing shift changes real take-up of a financial add-on cross-sell, where the "items" are services rather than products.

This experiment. It tests whether the identical total discount, stated once on a two-add-on bundle instead of once per add-on, increases how often customers take both.

Customers offered "save $2 when you bundle ID theft protection and device insurance together" take both add-ons more often than customers offered "save $1 off ID theft protection" and "save $1 off device insurance" as two separate line items, for the identical $2 total saving.

Illustrative, not real product data. Assume 11% of customers take both add-ons when the two discounts are shown separately, one per item.

The risk. A bundle framing that makes a saving feel bigger than it is could sell add-ons a customer wouldn't otherwise want, then get cancelled once the bill arrives and the framing has worn off.

The guardrail. The bundle discount must equal, not exceed, the sum of what the two item-level discounts would have been; no inflated "bundle-only" saving may be invented to make the framing test unfairly favourable.

What's being tested. Whether the framing itself changes take-up for an identical real saving, not whether a bundle can be priced to look better than it is. See Not Testing Is Still a Bet.

The study. Bertrand and Morse ran a real field experiment inside 77 payday loan stores, randomising 1,441 real borrowers to a control group or one of several disclosure formats shown at the counter. An APR figure, and a comparison to credit-card APRs, barely moved anything. A format that instead named the real dollar fees a borrower would accumulate if the loan renewed repeatedly cut their borrowing over the following four months by about 11%.

The gap. That disclosure was delivered by a person, on paper, at a physical counter, for a payday loan. Nobody has tested whether the identical format, a real dollar-fees-over-time figure, delivered inside a digital checkout screen instead of by a person, moves behaviour the same way for Buy Now, Pay Later, a product built around exactly the repeat, compounding late fee the original study measured.

This experiment. It tests the same decision Bertrand and Morse tested: an existing high-cost-credit borrower's next borrowing decision, not whether to complete the purchase in front of them right now. The dollar-cost figure is tied to the current order's own real terms, a projection, not a personal history lookup, mirroring exactly what the original disclosure format showed.

Existing BNPL users with at least one prior late payment, shown the real dollar late-fee cost of missing payments on their current order at the moment they confirm it, go on to miss fewer payments and take out fewer new BNPL purchases over the following months than users shown only the standard terms link.

Illustrative, not real BNPL provider data. Assume 24% of users with a prior late payment miss a payment again on their next order when shown only the standard terms link.

The line. Showing a real dollar-cost projection to someone who has already missed a payment is not a neutral change, so the restraint is worth stating before the design. This isn't built to talk anyone out of BNPL when it fits how they actually intend to pay. Plenty of BNPL purchases are paid on time and cost nothing extra.

The restraint. The figure shown is a real projection tied to the current order's own instalment terms, never an invented worst case, and it appears alongside the purchase, not in place of it: nothing about the checkout flow itself is slowed down or blocked.

The risk this specifically guards against. The whole reason to test this rather than assume it works is Disclosure Backfire: disclosure doesn't reliably help just because it's honest. A late-fee warning that reads as an accusation, or that pushes a borrower towards a less transparent product instead of paying more carefully, would be the intervention backfiring, not succeeding.

The studies. Peck and Shu found that physically touching an object, even briefly, raises how much a person values it and how much they'll pay for it. Atasoy and Morewedge found the same underlying mechanism running the other direction: identical content is valued and paid for less once it becomes a purely digital good, because a digital copy generates a weaker sense that it's “mine.”

The gap. Both studies tested everyday consumer objects and generic digital content: mugs, sunglasses, souvenir photos, books, films. Neither tested a recurring benefit mailer tied to an actual, dated renewal decision for a paid product. Whether the same physical-ownership effect shows up in real renewal behaviour, months after the object arrived, is untested.

This experiment. It tests one level up from a lab object: a premium credit card's own annual member guide, sent either as a printed booklet or as a digital-only equivalent inside the app, with renewal at the card's next annual fee date as the real outcome.

Cardholders who receive a printed annual member guide, in addition to the digital version every cardholder already gets in the app, will report higher perceived value of the card at 90 days and renew at a higher rate at their next annual fee date, compared with cardholders who receive the digital-only version.

Illustrative, not real card-programme data. Assume the premium card's current annual renewal rate is 85%, with the digital-only guide as the existing standard.

The line. A physical mailer costs materially more per cardholder than a push notification. Testing it against a cheaper default is a fair comparison. But only if the digital-only arm still gets the full, real content, not a deliberately thinner version built to make print look better by comparison.

The restraint. Both arms receive identical content. The only difference is the medium the guide arrives in, and every cardholder still gets the in-app digital version regardless of which arm they're in.

The risk this specifically guards against. A cardholder who notices peers received a printed booklet and they didn't could read the difference as being treated as a lesser member, an unfairness read this site covers under Perceived Fairness. The complaint-rate guardrail below exists to catch that directly.

The study. Benartzi and Thaler found retirement savers roughly split their contributions evenly across however many funds their employer's plan happened to list, and the resulting stock/bond mix tracked the mix of funds on offer far more closely than any stated risk preference.

The gap. That's field data from employer-chosen 401(k) menus, not a menu a product team can freely redesign and re-test inside its own app, and it predates today's single-screen, pick-as-many-as-you-like investing menus like CommSec Pocket's own. No test yet checks whether trimming a real investing app's own option list changes how evenly a real user's first contribution ends up spread across whatever they pick.

This experiment. It tests whether replacing a flat, 10-option "Invest in" menu with a curated set of 3 pre-grouped options, each already diversified inside itself, changes how many portfolios a new user selects and whether the resulting split across them still tracks pure equal-weighting by count, inside the same signup flow, for the same app.

New users shown the trimmed, 3-option menu are more likely to end up with a genuinely diversified first portfolio than users shown the original 10-option menu, even though both groups still tend to split their money close to evenly across however many options they pick. The 10-option group is more likely to unintentionally overweight several overlapping single-country or single-theme funds by picking, say, 4 of the 10 and splitting evenly across them.

Illustrative, not real/disclosed data. Assume 45% of new signups shown the existing 10-option menu end up with a first-session portfolio classified as genuinely diversified, spanning at least two distinct, non-overlapping asset classes rather than several near-duplicate single-country or single-theme picks split evenly.

The guardrail. The test can only change how options are grouped and how many are shown by default, never nudge a user toward investing more than they intended or hide a legitimate option's existence entirely. Every option in the original 10-item menu must stay reachable through the curated screen, just organised differently, and any "already diversified" curated option must actually be diversified, not marketed as such while concentrated.

What's being tested. Whether restructuring the menu reduces the accidental overlap naive equal-weighting produces, not whether a shorter, more persuasive menu can funnel new users into house-preferred, higher-fee products. See Not Testing Is Still a Bet.

The study. Khan and Dhar had people first imagine committing to volunteer work, then choose between two equally-priced products, one practical, one indulgent. Imagining the virtuous act shifted choice toward the indulgent option compared with people given no such prompt first, evidence that a completed (or even merely imagined) responsible act can license a later indulgence.

The gap. The reward-redemption experiment already on this site tests this mechanism on a small, already-earned resource, points, choosing between two redemptions of equal value. Nothing on this site tests it on new money entering someone's life: a real lump sum with no assignment yet, and a real choice about whether it goes toward debt.

The prediction. If confirming a virtuous act is what does the licensing, not just the act itself, then two customers whose refund is applied to their card balance identically should still end up spending differently, depending only on whether the app told them so.

Among customers already enrolled in an automatic Refund Auto-Payoff feature, customers who receive an explicit confirmation that their tax refund was applied to their credit card balance show a bigger rise in discretionary card spending over the following 30 days than customers whose identical refund is applied to their balance without any distinct confirmation, just a line in their ordinary transaction history.

Illustrative, not real product data. Assume 40% of customers whose refund is applied without a distinct confirmation show a rise in discretionary card spend above their own prior 30-day average in the month that follows, ordinary post-windfall spending, refund or no confirmation.

The risk. A bank has a real financial interest in this specific finding: a confirmation message that increases discretionary spending after a debt paydown is a way to win back, in interest and fees, some of what the customer just saved. That incentive makes it tempting to design the confirmation to maximise the effect rather than to honestly inform the customer.

The guardrail. The underlying paydown is identical and unaffected in both arms; every enrolled customer's refund is applied to their balance the same way regardless of which arm they land in. Only whether they're told about it, not whether it happens, its size, or its timing, is being tested. The confirmation message itself states only true, specific facts, the dollar amount applied and the new balance, with no added encouragement to spend, celebrate, or reward the moment.

What's being tested. Whether making a real debt reduction visible changes later spending, not whether the confirmation should be redesigned to push that spending further. See Not Testing Is Still a Bet.

The study. Solnick and Hemenway asked people to choose between two hypothetical worlds: earning $50,000 while others earned $25,000, or earning $100,000 while others earned $200,000. A majority picked the world with less money outright, as long as it left them ahead of everyone around them.

The gap. That study was a hypothetical survey with no real money and no real product on the other end of the choice. Nothing on this site tests whether the same pull shows up when the two options are real, dollar-denominated financial products a customer could actually pick.

The prediction. If relative standing carries real weight in an actual purchase decision, adding a truthful peer benchmark to two unchanged cashback rates should move some customers off the higher-paying card and onto the one that merely ranks better.

Hypothesis. Among customers choosing between two real cashback rates on their own card spend, customers who are also shown a truthful benchmark of what similar-spend customers typically earn choose the lower-rate card at a higher rate than customers shown the same two rates with no benchmark.

Illustrative, not real product data. Assume 6% of customers pick the lower-rate card when shown only the two rates, most likely people choosing on a card feature other than cashback, rather than misreading the numbers.

The risk. A card issuer earns more margin on the lower-cashback card. A rank benchmark that pulls customers toward it, dressed up as helpful context, would cost real customers real money for the issuer's benefit.

The guardrail. Both rates are real, unchanged card products either arm could choose without this test running at all. The benchmark shown is a real, independently computed figure, not a number tuned to produce the result, and it's calculated the same way in both arms; only whether it's displayed differs.

What's being tested. Whether visible relative standing shifts a real choice away from the higher-paying option, not whether that shift should be built into how the cards are sold. See Not Testing Is Still a Bet.

The study. John, Blunden and Liu found that people who deliver bad news get rated less likeable, even when a random process, not the messenger, produced the outcome. The penalty shrank when the messenger explicitly signalled a benevolent motive while delivering the news.

The gap. That effect was shown for a person delivering news to another person. A loan decline is usually the opposite: a templated, automated message with no human messenger at all. Nothing on this site tests whether benevolence-framing still works when the “messenger” is a system-generated letter.

The prediction. If genuine care in the delivery softens the penalty even for a live human messenger, adding an explicit, honest statement of care to an otherwise identical automated decline should soften how a declined applicant feels about the bank, without changing the decision itself at all.

Hypothesis. Among applicants who receive an identical loan decline, same underlying decision, same reason codes, applicants whose decline opens with an explicit, genuine statement of care report less negative sentiment toward the bank on a short post-decision survey than applicants who receive the current generic decline message.

Illustrative, not real product data. Assume 34% of applicants who receive the current generic decline rate their experience 1 or 2 stars out of 5 on a short post-decision survey.

The risk. A bank has an interest in fewer complaints and better sentiment scores, regardless of whether the underlying decision was actually fair. Warmer language could be used to make a bad or biased decision feel better instead of making the decision itself better, or to quietly discourage a customer with a real grievance from escalating it.

The guardrail. The underlying credit decision, the reason codes shown, and the applicant's appeal rights are identical in both arms; only the opening framing sentence changes. That sentence states only true things, real next steps and real resources, and never implies the decision could change just by asking.

What's being tested. Whether framing changes how a customer feels about an unchanged decision, not whether framing should be used to reduce complaints about decisions that are actually wrong. See Not Testing Is Still a Bet.

The study. Gollwitzer and Brandstätter found that specifying exactly when and where you'll act on a goal makes you far more likely to actually follow through than holding the same goal without a specific plan.

The gap. CommBank's real appointment flow (commbank.com.au/appointment) lets a customer book a home loan appointment by phone or in-branch. Both already tell the customer everything an implementation intention would need: the confirmed time, and exactly what to have ready. But it's all stated to the customer, never asked back. An in-branch appointment also carries a barrier a phone call never has: actually getting to a specific address on time.

This experiment. It tests four different ways of asking for a plan on the confirmation screen. One names a vivid, specific moment. One has the customer state the whole plan back in their own words. One names what might get in the way and plans around it. One is a light, optional suggestion with nothing to fill in. Running the identical four against both a phone appointment and an in-branch appointment separates two real questions. Which approach works at all, and whether the same one works as well for a remembering problem as it does for a travelling one.

Hypothesis. Among customers who book a home loan appointment, by phone or in-branch, customers shown any of the four confirmation-screen prompts show a lower no-show rate than customers who are only ever told the details. Whether the four prompts rank the same way for both appointment types is a separate question. A travelling problem might call for a different one of them than a remembering problem does, and that's itself part of what this experiment would show.

Illustrative, not real CommBank data. Assume 22% of booked home loan phone appointments end in a no-show under the current reminder-call script.

Illustrative, not real CommBank data. Assume 28% of booked in-branch home loan appointments end in a no-show, higher than the phone rate, since travelling somewhere by a set time is a real added barrier a phone call never has.

The risk. A prompt that presumes a specific time, travel mode or personal obstacle can feel intrusive if it asks for more than a customer wants to give before they've even arrived. A prompt with no real payoff to the customer can also read as the bank telling them what to think, rather than helping them plan something they'd genuinely benefit from planning.

The guardrail. The appointment, the specialist or branch, and the actual information required are identical across all five arms, whichever appointment type is shown. Every confirmation-screen prompt is optional and skippable, any options it offers are neutral and non-exhaustive, and none of them presume which obstacle, travel mode or moment matters most to a given customer.

What's being tested. Whether asking the customer to state their own plan changes follow-through on an identical appointment, not whether the confirmation screen or reminder call itself should exist. See Not Testing Is Still a Bet.

The reminder-fatigue risk. The reminder call itself carries a real, separate cost this experiment doesn't measure: repeated contact can lift today's response while quietly raising how many customers opt out of future contact altogether. See Reminder Fatigue.